NBER WORKING PAPER SERIES

GENERAL EQUILIBRIUM EFFECTS OF CASH TRANSFERS: EXPERIMENTAL EVIDENCE FROM KENYA

Dennis EggerJohannes Haushofer

Edward MiguelPaul Niehaus

Michael W. Walker

Working Paper 26600http://www.nber.org/papers/w26600

NATIONAL BUREAU OF ECONOMIC RESEARCH1050 Massachusetts Avenue

Cambridge, MA 02138December 2019, Revised October 2021

Niehaus is a co-founder, former president (2012 - 2017) and chairman (without compensation) of the board of GiveDirectly. Haushofer is the founder and a board member (uncompensated) of the Busara Center for Behavioral Economics. We thank the study participants for generously giving their time; Justin Abraham, Aakash Bhalothia, Christina Brown, Genevieve Deneoux, Tilman Graff, Max Lauletta, Michelle Layvant, Layna Lowe, Anya Marchenko, Gwyneth Miner, Max Mueller, Priscilla de Oliviera, Robert On, Rachel Pizatella-Haswell, Emaan Siddique, Zenan Wang, Francis Wong and Kejian Zhao for excellent research assistance; Innovations for Poverty Action for data collection fieldwork; the Busara Center for Behavioral Economics for piloting work; GiveDirectly for fruitful collaboration; and Martin Aragoneses, Vittorio Bassi, Abhijit Banerjee, Chris Blattman, Giacomo DiGiorgi, Esther Duflo, Yuriy Gorodnichenko, Seema Jayachandran, Adriana Lleras-Muney, Atif Mian, Emi Nakamura, Ben Olken, Jon Steinsson, numerous conference and seminar participants, and three anonymous referees and the Editor (D. Donaldson) for comments. This research was supported by grants from the National Science Foundation, International Growth Centre, CEPR/Private Enterprise Development in Low-Income Countries (PEDL), the Weiss Family Foundation, and an anonymous donor. The GiveDirectly program was supported by The Pershing Square Foundation. Walker gratefully acknowledges financial support from the NSF Graduate Research Fellowship (Grant No. DGE 1106400). The study received IRB approval from Maseno University and the Univ. of California, Berkeley. AEA Trial Registry RCT ID: AEARCTR-0000505.

NBER working papers are circulated for discussion and comment purposes. They have not been peer-reviewed or been subject to the review by the NBER Board of Directors that accompanies official NBER publications.

© 2019 by Dennis Egger, Johannes Haushofer, Edward Miguel, Paul Niehaus, and Michael W. Walker. All rights reserved. Short sections of text, not to exceed two paragraphs, may be quoted without explicit permission provided that full credit, including © notice, is given to the source.

General Equilibrium Effects of Cash Transfers: Experimental Evidence from KenyaDennis Egger, Johannes Haushofer, Edward Miguel, Paul Niehaus, and Michael W. WalkerNBER Working Paper No. 26600December 2019JEL No. E62,H3,O12,O23,R13

ABSTRACT

How large economic stimuli generate individual and aggregate responses is a central question in economics, but has not been studied experimentally. We provided one-time cash transfers of about USD 1000 to over 10,500 poor households across 653 randomized villages in rural Kenya. The implied fiscal shock was over 15 percent of local GDP. We find large impacts on consumption and assets for recipients. Importantly, we document large positive spillovers on non-recipient households and firms, and minimal price inflation. We estimate a local transfer multiplier of 2.4. We interpret welfare implications through the lens of a simple household optimization framework.

Dennis EggerUniversity of California, BerkeleyDepartment of Economics530 Evans Hall #3880Berkeley, CA 94720-3880dennistegger@berkeley.edu

Johannes HaushoferDepartment of EconomicsStockholm UniversityUniversitetsvägen 10 AStockholm 106 91 Swedenand Busara Center for Behavioral Economics,Nairobi, Kenyaand also NBERjohannes.haushofer@ne.su.se

Edward MiguelDepartment of Economics University of California, Berkeley 530 Evans Hall #3880Berkeley, CA 94720and NBERemiguel@econ.berkeley.edu

Paul NiehausDepartment of EconomicsUniversity of California, San Diego9500 Gilman Drive #0508La Jolla, CA 92093and NBERpniehaus@ucsd.edu

Michael W. WalkerUniversity of California, BerkeleyCenter for Effective Global Action714B Giannini HallBerkeley, CA 94720 mwwalker@berkeley.edu

A randomized controlled trials registry entry is available at https://www.socialscienceregistry.org/trials/505 An appendix is available at http://www.nber.org/data-appendix/w26600

1 Introduction

Tracing out the pattern of transactions in an integrated economy, and their contribution

to aggregates of interest like overall output or well-being, has long been a central task of

economic analysis. For instance, there has been interest in understanding the aggregate

impacts of fiscal stimulus and cash infusions for decades (Keynes 1936), and a growing

body of empirical evidence from rich countries shows that fiscal multipliers can sometimes

be positive and large, based on non-experimental variation generated by policy changes

(Chodorow-Reich 2019; Nakamura and Steinsson 2014; Suarez Serrato and Wingender 2016;

Auerbach, Gorodnichenko, and Murphy 2020). Until now, however, these issues have not

been subjected to experimental examination.

There is also renewed interest in related topics in development economics with the rise of

large-scale cash transfer programs, which have now been implemented in scores of low and

middle income countries.1 A large literature on the impacts of these transfers has developed,

employing well-identified experimental and quasi-experimental designs. These studies have

documented effects on a broad range of behavioral responses among treated households,

including consumption, earnings, assets, food security, child growth and schooling, self-

reported health, female empowerment, and psychological well-being (Haushofer and Shapiro

(2016), Baird, McIntosh, and Ozler (2011), and Bastagli et al. (2016)). Yet there is limited

evidence on the aggregate economic impacts or welfare consequences of such policies (for

exceptions, see Angelucci and De Giorgi (2009), Cunha, De Giorgi, and Jayachandran (2018),

and Filmer et al. (2018)).

The present study was prospectively designed to unite these two disparate literatures

by experimentally studying the aggregate impacts of large cash stimulus programs. We

designed and carried out a large-scale experiment in rural Kenya that provided one-time

cash transfers worth roughly USD 1000 (distributed by the NGO GiveDirectly) to over

10,500 poor households in a sample of 653 villages with a population of roughly 300,000.

The implied fiscal shock was large, as the cash transfers amounted to over 15% of GDP in

treatment villages during the peak 12 months of the program.

Beyond its fiscal scale, at least three aspects of the project represent advances on most

existing work. First, we generated substantial spatial variation in the intensity of transfers

by deliberately randomizing the allocation of cash transfers not just across households or

villages (as is typical), but also across geographic sublocations (groups of 10–15 villages),

thereby increasing our ability to detect aggregate impacts. Second, we carried out unusually

1. 97% of developing countries in Europe, Latin America and Sub-Saharan Africa have some type of cashtransfer program (World Bank 2017).

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extensive original data collection, giving us greater visibility into the chain of causal effects

linking cash transfers to aggregate outcomes in a complex and interconnected economy. Our

household and enterprise censuses of the study area count 65,385 households and 12,095 non-

farm enterprises. Within this unusually large sampling frame, we gathered detailed panel

(longitudinal) data on household receipt of the transfer; household consumption expenditure

patterns (representative for both recipient and non-recipient households); local enterprise

production, employment and revenue; labor market conditions; as well as especially high-

frequency (monthly) and spatially disaggregated market data on prices. Third, we interpret

the results through the lens of a theoretical framework that highlights the links between the

individual empirical results, the aggregate transfer multiplier, and welfare in this setting.

Following earlier studies, we first document large direct impacts on households that

received transfers, including increases in consumption expenditures and holdings of durable

assets eighteen months after the start of transfers. We do not observe meaningful changes

in total labor supply among recipient households.

Enterprises in areas that receive more cash transfers also experience meaningful revenue

gains, in line with the increases in household expenditure. Interestingly, sales increased with-

out noticeable changes in firm investment behavior (beyond a modest increase in inventories),

and did not increase differentially for firms owned by cash recipient households relative to

non-recipients. Both patterns suggest a demand- rather than investment-led expansion in

economic activity. Increased enterprise revenue in turn translates into moderate increases

in wage bills and profits. Methodologically, one important feature of the enterprise (and to

a lesser extent household) results is that they are largely driven by the overall intensity of

treatment in nearby communities, not solely by the treatment status of the village in which

the enterprise is located. This suggests that common study designs which aim to identify

spillover effects by clustering treatment at the village level and assuming no spillovers across

villages may be mis-specified, at least in densely populated areas such as the one we study.2

Despite not receiving transfers, non-recipient households also exhibit large consumption

expenditure gains: their annualized consumption expenditure is 13% higher eighteen months

after transfers began, an increase roughly comparable to the gains contemporaneously expe-

rienced by the recipient households.3 Increased spending is not financed by dissaving, but

more likely results in part from the income gains experienced by local firms’ owners and

workers. Indeed, non-recipients’ income gain is driven largely by increases in wage labor

earnings, consistent with the fact that enterprise wage bills increase. In a reassuring check,

2. For example, households are located within 2 km of seven other villages on average.3. We note below that consumption gains among recipient households are likely to have been larger in the

period immediately following transfer receipt.

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the magnitude of per capita consumption gains among local households lines up roughly

with the per capita revenue gains among local firms. On some level this is unsurprising, as

increases in local consumption expenditures were spent somewhere; our contribution is to

carefully document how such spending spreads locally through a low-income economy.

A further issue is the extent to which transfers affect local prices (as for example Cunha,

De Giorgi, and Jayachandran (2018) show in Mexico), and thus the extent to which the

effects described above are nominal or real. We study this question through careful monthly

measurement of prices for scores of local commodities, consumer goods, and durable goods,

as well as prices for inputs like labor and capital. For inputs, we find positive point estimates,

but they are economically moderate in magnitude and not always statistically significant.

For outputs, we document statistically significant, but economically minimal, local price

inflation. Average price inflation is 0.1%, and even during periods with the largest transfers,

estimated price effects are less than 1% and precisely estimated across all categories of goods.

We next ask what these effects imply for the aggregate level of economic activity, com-

puting a local transfer multiplier. A standard macroeconomic framework would predict that

large multipliers are possible in our rural Kenyan setting: it is a largely closed local economy

within a currency union receiving external transfers, with incomplete markets and a large

share of hand-to-mouth consumers (Farhi and Werning 2016). Using an expenditure-based

approach that takes advantage of our data on the consumption expenditures of representa-

tive samples of both recipient and non-recipient households as well as investment by local

firms, we estimate a local transfer multiplier of 2.5. A dual income-based approach, relying

on distinct and complementary measures of labor and capital income, enterprise profits, and

taxes, yields a similar estimate of 2.3. These estimates are broadly in line with what a sim-

ple model would imply from households’ marginal propensity to consume local value added,

which we estimate to be approximately 0.76 over the study period. These results contribute

to an active recent empirical literature that estimates multipliers.4

A core contribution of this study is thus to exploit a randomized experiment to estimate

an important macroeconomic quantity (see Muralidharan and Niehaus (2017) for a related

discussion). A notable aspect of our approach is the fact that transfers came from donors out-

4. Our estimates are somewhat larger than those from a structural simulation, which predicted that thelocal multiplier from cash transfers in rural Kenya could range from 1.6 to 1.9 (Thome et al. 2013), andare similar in magnitude to non-experimental estimates from a cash transfer program in Mexico (1.5 to2.6) (Sadoulet, Janvry, and Davis 2001). They are also somewhat larger than recent estimates of the fiscalspending multiplier (which is distinct from the transfer multiplier, since households can save part of thetransfer) derived from cross-sectional US policy variation, which often range from 1.5-2.0 (Chodorow-Reich2019), and from Brazil, which are close to 2 (Corbi, Papaioannou, and Surico 2019). Pennings (2021) focuseson the US transfer multiplier. Kraay (2014) estimates fiscal multiplier estimates less than one when donorlending is used as an instrument for national government spending in developing countries.

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side the study area, rather than being internally tax- or debt-financed; the latter is typically

the case in the US programs studied, and may complicate the interpretation of consump-

tion responses due to contemporaneous tax incidence or Ricardian equivalence issues. The

targeting of the transfers to just one region within the larger Kenyan economy also allows

us to abstract away from monetary policy and exchange rate responses, simplifying analysis

relative to the study of national stimulus policies. A limitation of our approach is that we

observe partial data in the months immediately following the transfers, which reduces the

precision of some estimates.

Few existing treatments of multipliers also explicitly examine their welfare implications.5

We interpret the welfare implications of our results using a simple theoretical framework.

Transfers directly increase the welfare of those who receive them by $1 per $1 received. Gen-

eral equilibrium effects impact welfare through two additional channels: changes in household

budget sets (due for example to changes in wages, prices, or firm profits), and changes in

peer behaviors that enter directly into own utility (due to externalities or public good pro-

vision). The value of budget set expansions depends on what drives them: expansions due

to increases in productivity are worth $1 per $1, while expansions due to increased factor

supply (e.g., labor) come at a partially offsetting opportunity cost. Interpreted through this

lens, the results generally suggest that non-recipients were made better off by an expansion in

their budget sets driven largely by increased factor productivity, as opposed to factor supply.

Externality effects are positive or null, with one possible exception: positive spillovers were

large enough that village-level asset inequality increased slightly, which may affect well-being

if households have preferences over their relative socioeconomic standing.

The constellation of findings raises an intriguing question about how the economy ab-

sorbed such a large shock to aggregate demand, and in particular how it did so without

correspondingly large increases in the employment of land (which is in fixed supply), labor,

or capital. One plausible, albeit speculative, possibility is that the utilization of these fac-

tors was “slack” in at least some enterprises (Lewis 1954). This seems plausible because in

the retail and manufacturing sectors, where output responses were concentrated, the typical

firm has a single employee (i.e., the proprietor), suggesting that integer constraints may often

bind. In addition, many enterprises operate “on demand” in the sense that they produce

only when they have customers, and the average non-agricultural enterprise sees just 1.9

customers per hour. In addition to retail, much manufacturing in this setting is on demand;

for example, a mill owner waits for customers to bring their grain. The existence of slack

may help account for the large multiplier we estimate, as has also recently been argued in

US data (Michaillat and Saez 2015; Murphy 2017).

5. Recent and notable exceptions include Mankiw and Weinzierl (2011) and Sims and Wolff (2018).

4

2 Study design

2.1 Setting: rural western Kenya

The study took place in three contiguous subcounties of Siaya County, a rural area in western

Kenya bordering Lake Victoria. The population in Siaya is predominantly Luo, the second

largest ethnic group in Kenya, and while rural it is also relatively densely populated, with

395 people per km2 compared to a Kenyan average of 91. The main national road running

from the port of Mombasa to Nairobi and on to Kampala passes through the study area,

likely helping to integrate it into the regional economy.

The NGO GiveDirectly (GD) selected the study area based on its high poverty levels.

Within this area GD selected rural (i.e., not peri-urban) villages in which it had not previ-

ously worked.6 This yielded a final sample of 653 villages spread across 84 sublocations (the

administrative unit above a village). The mean village consists of 100 households, and at

baseline, the average household had 4.3 members, of which 2.3 were children. The average

survey respondent was 48 years old and had about 6 years of schooling. 97% of house-

holds were engaged in agriculture; at endline, 49% of households in control villages were also

engaged in wage work and 48% in self-employment.

Transfers and data collection took place from mid-2014 to early 2017, a period of steady

economic growth, relative prosperity, and political stability in Kenya. The World Bank

reports annual per capita GDP growth rates ranged between 2.4 to 3.4 percent. All data

collection concluded months prior to the August 2017 national election.

2.2 Intervention: The GiveDirectly (GD) Cash Transfer Program

GD provides unconditional cash transfers to poor households in low-income countries. For

the purpose of this study, to be eligible for transfers, households had to live in homes with

thatched roofs, a simple means-test for poverty. In treatment villages, GD enrolled all

households that met this criterion (“eligible” households) as classified by their field staff

through a village census, and confirmed via two additional visits (see Appendix B.1).

Approximately one-third of all households were eligible. These households received a

series of three transfers totaling KES 87,000, or USD 1,871 PPP (USD 1,000 nominal),

via the mobile money system M-Pesa, which is widely used in Kenya. (Registering for M-

Pesa was a prerequisite for receiving transfers; households without a mobile phone were

given the option to purchase one from GD staff with the cost deducted from their transfer.)

Households selected the member they wished to receive the transfers. The total transfer

6. The listing of villages was based on the 2009 National Population Census; enumeration areas (whichtypically correspond to a single village) were treated as villages by GD and this study.

5

is large, corresponding to 75 percent of mean annual household expenditure in recipient

households. In aggregate, the transfers were equivalent to approximately 17 percent of

annual GDP (based on our data described below) in the treated areas during the peak 12

months of disbursements, and to 24 percent of annual GDP during the full 24 month rollout

period. Although small in relation to overall Kenyan GDP in 2015 (ă0.1%), locally this

is thus a larger relative shock than most government transfer programs, e.g., the ARRA

programs studied in the recent US fiscal multiplier literature, see Chodorow-Reich (2019).

Transfers were made in a series of three payments as follows: a token transfer of KES

7,000 (USD 151 PPP) was sent once a majority of eligible households within the village had

completed the enrollment process, followed two months later by the first large installment

of KES 40,000 (USD 860 PPP). Six months later (and eight months after the token trans-

fer), the second and final large installment of KES 40,000 was sent. The median treated

household received its token transfer 47 days after being registered for the program; trans-

fers should be interpreted as anticipated during that period to the extent recipients believed

GD’s promises.7 The transfers were non-recurring, i.e., no additional financial assistance was

provided to recipient households after their final installment, and they were informed of this

up front. Households in control villages did not receive transfers.

2.3 Experimental design

To identify spillovers both within and across villages, we employed a two-level randomization

design (Figure A.1, Panel A). First, we randomly assigned sublocations (or in some cases,

groups of sublocations) to high or low saturation status, resulting in 33 high- and 35 low-

saturation groups. Within high (low) saturation groups we then randomly assigned two-

thirds (one-third) of villages to treatment status. We also randomized the order in which

treatment was rolled out to treated villages. Within treatment villages, all eligible households

received a transfer.8 This design induces variation in treatment intensity across space due

both to the variation in sublocation treatment intensity, and random variation in the location

of treated villages within sublocations. Figure A.2 illustrates that there is considerable

7. The precise timing of the first transfer was uncertain, and we believe that recipients may also haveperceived the first transfer as less certain than the subsequent ones. However, we do not know of anyborrowing against future GD payments, and credit markets are imperfect in our context. In the earlierGiveDirectly study, Haushofer and Shapiro (2016) find evidence for both savings and credit constraints:households that received lump-sum transfers were more likely to own large durable assets at endline thanhouseholds receiving monthly transfers, even though the total transfer amounts were the same. This suggeststhat households had trouble borrowing against the promise of the future transfer and saving the earlyinstallments. This is also consistent with US evidence finding no anticipation in advance of the receipt ofeconomic stimulus payments (Broda and Parker 2014). We therefore consider all transfers symmetrically inour dynamic regressions and leave analysis of potentially differing effects across installments for future work.

8. Full details of the randomization are in Appendix B.2.

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variation both across and within sublocations in the share of neighboring villages treated.9

3 Data and empirical specifications

We conducted four types of surveys, of households, enterprises, market prices, and local

public goods. Results from the public goods surveys are presented primarily in a separate

paper (Walker 2018), and discussed briefly here. We filed several pre-analysis plans for this

project; for details on the PAPs and where we go beyond these plans, see Appendix I.

3.1 Household data

We first conducted a baseline household census in all villages, which serves as a sampling

frame and classifies household eligibility status. The census was designed to mimic GD’s

censusing procedure but was conducted by independent (non-GD) enumerators across both

treatment and control villages for consistency. Throughout this paper, we base our analysis

on village membership, household definitions and eligibility as classified by our project data

collection field staff. In all, the census identified 65,385 households with a total baseline

population of 280,000 people in study villages.

We conducted baseline household surveys within one to two months after the census and

before the distribution of any transfers to a village (Figure A.1, Panel B).10 We used census

information to sample at random eight eligible and four ineligible households per village to

survey. When households contain a married or cohabiting couple, we randomly selected one of

the partners as the target survey respondent. Due to time and budget constraints, we sought

to complete all baseline household surveys in a single day. If a household on our sampling

list was not available on that day, we instead surveyed a randomly-selected replacement

household with the same eligibility status. We conducted a total of 7,848 baseline household

surveys between September 2014 and August 2015.11 The survey contained detailed modules

on economic activities, asset ownership, psychological well-being, health and nutrition. A

large array of baseline characteristics are balanced across treatment and control villages

(Table C.2, column 2).

Endline household survey data was collected between 9 and 31 months after each house-

hold’s “experimental start date,” meaning the month in which transfers were expected to

9. Figure B.1 provides a higher-resolution example for two villages.10. In a few cases, baseline surveys were conducted before the distribution of transfers but after GD had

held meetings in the village informing households that it would be a treatment village.11. Of this total, 6,510 households were on the initial sampling list, and 1,338 were randomly-selected

replacement households.

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start in a village assigned to treatment, regardless of their actual treatment timing.12 The

5th/95th percentiles of timing ranged from 12 to 27 months, and the median survey was

conducted 19 months after the experimental start month, or about 11 months after the

distribution of the last lump sum transfer (Figure A.1, Panel B). This timing implies that

some but relatively few households were surveyed in the months immediately following cash

transfer receipt, an issue we return to below when estimating the transfer multiplier.

Endline household surveys targeted all households on the initial sampling lists (including

those missed at baseline), along with replacement households that were surveyed at baseline.

For households that had been surveyed at baseline, we attempted to survey the individual

who was the baseline respondent. We conducted a total of 8,242 endline household surveys

between May 2016 and June 2017.13 We achieved high tracking rates at endline, reaching

over 90% of eligible and ineligible households in both treatment and control villages, and

these rates do not systematically vary by treatment status (Table C.1). The only subgroup

difference of note is that we are slightly less likely to find ineligible households that were

initially surveyed at baseline in high saturation sublocations (see Appendix C.2 for more

information). In addition to the baseline modules, endline surveys collected more detailed

data on household expenditures and crop production, additional psychological scales (in par-

ticular, related to stress and hope), and female respondents surveyed by a female enumerator

were also administered a module on female empowerment and gender-based violence.

3.2 Empirics: recipient households

If the general equilibrium effects of transfers were fully contained within administrative units

(here, villages and sublocations), then an appropriate specification would be

yivs “ α1Treatv ` α2HighSats ` δ1yivs,t“0 ` δ2Mivs ` εivs, (1)

where yivs is an outcome of interest for household i in village v in sublocation s.14 Treatv

is an indicator for residing in a treatment village at baseline, and HighSats an indicator

for being in a high-saturation sublocation. Here α1 captures the total average treatment

12. The order in which villages were visited by GD and the research team was randomized within subcoun-ties. We calculate the start and end months of when GD started transfers to villages within a subcounty,and then, across these months, evenly assign both treatment and control villages experimental start monthsbased on the random ordering.

13. This includes 7,019 initially sampled and 1,223 replacement households. Of the initially sampled house-holds, 1,015 had been missed at baseline. The main analysis focuses on the “initially sampled” (which includesthose missed at baseline) and “replacement” households; results are similar using only originally sampledhouseholds (available upon request).

14. When we examine individual-level outcomes using Equation (1), we define treatment status and eligi-bility on the basis of the household in which the individual lives.

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effect for households in treatment versus control villages, including both the direct effect of

treatment (for eligible households) and any within-village spillovers; note that our design

does not allow us to identify these separately. α2 is a relatively coarse way to assess cross-

village spillovers, as it does not utilize all experimental variation. We include the baseline

value of the outcome variable (yivs,t“0), when available, to improve statistical precision.15

We cluster standard errors at the village level, and weight observations by inverse sampling

probabilities to be representative of the population of eligible households.

Overall, we view Equation 1 as a useful benchmark but unlikely to capture well the spatial

variation in treatment intensity evident in Figure A.2. This is because in our study area

villages are relatively close to each other; sublocation boundaries are not “hard” in any sense

nor reflective of salient ethnic or social divides; and because our data indicate that there

is extensive economic interaction in nearby markets regardless of sublocation. To better

capture spillovers, we therefore estimate models in which a household’s outcomes depend on

the amount of money distributed in its own and other geographically proximate villages:

yiv “ α ` βAmtv `Rÿ

r“2

βrAmt vv,r ` δ1yiv,t“0 ` δ2Miv ` εiv. (2)

The novel terms here are the amount Amtv of cash per capita transferred to one’s own village

v over the entire study, and the amount Amt vv,r of cash per capita transferred to villages other

than v in a series of bands with inner radius r ´ 2 km and outer radius r km around the

village centroid. We normalize both to be measured as a share of per capita GDP.16 The

Amt variables depend on both the random assignment of villages to treatment and also on

the endogenous share of households in those villages eligible for transfers, so we instrument

for them using the own-village treatment indicator Treatv and the share se,t v,r of eligible

households in each band assigned to treatment. For brevity, we do not report IV first-stage

results; however, the minimum first-stage Sanderson-Windmeijer F-statistic is 107.9 across

all the cross-sectional specifications (Tables 1-3) and 88.4 in the multiplier specifications

below, minimizing concerns about weak instruments. To account for spatial correlation, we

calculate standard errors using a uniform kernel up to 10 km (Conley 2008).17

15. For observations where the baseline value is missing, we include an indicator variable equal to onedenoting a missing value (Mivs), and set the baseline value of the outcome variable equal to its mean.

16. We use an expenditure-based measure of GDP that is described in Section 5, which we convert to aper-capita measure based on household census data from our study area, and augmented with data from theGiveDirectly census and the 2009 Kenya National Population Census when necessary. Per capita GDP inlow saturation control villages is 637 USD PPP (2727 USD PPP per household); see Appendix B.3.

17. We also conduct Fisher randomization tests for all specifications, where we re-randomize cash transfersacross sublocations and villages as well as their roll-out over time as in our experiment and test against thesharp null that effects are zero. Conclusions are robust to this alternative method of inference.

9

Because we had no a priori knowledge of the relevant distances over which general equi-

librium effects might operate, we pre-specified an approach in which we first estimate a

series of nested models varying the outer limit R of the spatial bands from 2 km to 20 km in

steps of 2 km, and then select the one which minimized the Schwarz Bayesian Information

Criterion (BIC). We report estimates of Equation (2) using the selected outer limit R. As it

turns out, this algorithm selects only the innermost 0–2 km band for almost all outcomes.18

Equation (2) correctly identifies the overall effects of the intervention if transfers delivered

outside the radius R have no effect on i. If not – if, for example, all households were affected to

some extent by all transfers in the study area – then the estimated effects are relative to these

“ambient” effects. The BIC selection procedure determines how reasonable this identifying

assumption is by omitting ring R ` 2 from the model if it has little explanatory power for

the outcome. In principle, this could be either because variation in treatment intensity at

that distance has a precisely estimated but small effect on the outcome (in which case it is

a good “control”), or because there simply is not much variation in treatment intensity at

that distance (in which case we cannot be sure). Given this, it is important to note that

our design generates substantial variation in treatment intensity even at larger distances.

Transfers in the 2 km buffer, which the BIC always includes, range from 0 to 27% of GDP,

with a 10-90 percentile range of [4%, 15%]. Even in the 4 to 6 km buffer, which the BIC

never selects for any primary outcome, the 10-90 percentile range remains wide, at [3%,

10%]. This suggests that a subset of our villages can reasonably serve as “pure controls.”

We also examine in Appendix F how sensitive our main conclusions are to fixing larger

maximal radii R than the BIC selects, which implies a more conservative definition of the

“control group.” While there is some variation from outcome to outcome, overall the effects

are quite stable as we add the 2-4 km band and fairly stable as we add the 4-6 km band,

though as expected standard errors often become much larger. We generally cannot reject

that these estimates are different statistically from those estimated using the BIC-optimal

bandwidth, giving us greater confidence in the latter. Finally, note that we typically estimate

spillovers of the same ‘sign’ as the direct effects, which suggests that any remaining bias in

our estimates likely leads us to understate, rather than overstate, overall effects. All told,

18. Note that this model selection step introduces some circularity, as we first determine the distancesat which effects occur, and then estimate effects at those distances. We check that inference is robust tothis model selection, and to alternative approaches more generally. First, we calculate exact p-values usinga Fisher permutation test (i.e. randomization inference, see Appendix F.4). Second, we conduct repeated50-50 splits of the data into training and test sets, using the training data from each split to perform the BICstep and the test set to estimate parameters, and record the proportion of times that the resulting estimateslie within the 95% confidence intervals we report here (Appendix F.2). Third, we estimate effects holdingthe spatial radius fixed at 2 km, 4 km, and 6 km, respectively, thus eliminating the model selection step(Appendix F.1). Taken together, these results provide reassurance that our methods yield valid inferences.

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we view the problem of estimating spatial effects as unlikely to admit a perfect solution, but

believe that our study design and econometric specification allow us to advance meaningfully

relative to most existing work.

We estimate Equation (2) for all eligible households and then use it to obtain estimates

of the total effect on recipient households, which we report as “Recipient Households” in

tables. By “total effect” we mean how the households’ outcomes differ from what they

would have been in the absence of the intervention. We calculate these by multiplying

the estimated coefficients from Equation (2) by the average values of the regressors, i.e.,

β ¨`

ĘAmtv|i is an eligible recipient˘

`řRr“2 βr ¨

`

ĘAmt vv,r|i is an eligible recipient

˘

for all radii

bands up to the selected R. This effect allows for across-village spillovers in addition to

direct effects and within-village spillovers.19 As a benchmark, we also report estimates of α1

from Equation (1), which is the total treatment effect if all spillovers are contained within

villages (a common identifying assumption).

3.3 Empirics: non-recipient households

We use an analogous approach to estimate total effects on non-recipient households, which

include both eligible households in control villages and ineligible households in all villages.

Specifically, we estimate

yiv “ α `Rÿ

r“2

β1rAmtv,r `

Rÿ

r“2

β2r pAmtv,r ¨ Eligivq ` γEligiv ` yiv,t“0 ¨ δ ` εiv. (3)

This specification modifies Equation (2) as follows. First, because non-recipient households

do not experience direct effects, we no longer separate own-village effects and across-village

spillovers: we drop Amtv and replace Amt vv,r with Amtv,r, so that spillovers work entirely

through β1r and β2

r . Second, we include an indicator for eligibility status and its interaction

term with amounts to allow for spillovers to differ by eligibility status (recall that eligible

households in control villages are non-recipients). As above, we instrument for Amtv,r using

the share of eligible households assigned to treatment within the corresponding band, i.e.,

se,tv,r and se,tv,r ¨ Eligiv for each radii band v. When available, we include the baseline value of

the outcome variable. We report the average total effect on non-recipients as a population-

19. Appendix C.5 provides an example of this for outcomes in Table 1. We also consider the possibilitythat effects are non-linear in the per-capita amounts transferred. Figure A.3 presents non-linear estimatesof equation 2 for two key outcomes, total consumption and firm revenue. The relationships appear roughlylinear, and we cannot formally reject linearity. We conduct the same test for our 10 pre-specified primaryoutcomes and eligible / ineligible households separately, and cannot reject linearity at the 10% significancelevel for any of them.

11

weighted average of effects for the two groups.20

3.4 Enterprise data

We employ several complementary sources of data on enterprises. First, we use detailed agri-

cultural and self-employment modules from the household surveys. The agriculture module

covers crop-by-crop agricultural production, sales, employment, and input costs; the self-

employment module covers revenues, profits, hours worked, and some costs and investments

for enterprises run by household members. These data are representative of enterprises

owned locally (i.e., by residents of the study area) and allow us to clearly attribute profits

to their residual claimants. They do not capture enterprises owned by people living outside

the study area, which we capture separately through the enterprise census and surveys.

Specifically, we conducted censuses and surveyed a representative subset of all non-farm

enterprises at baseline and endline (see Appendix D for details). The endline census was

conducted between November 2016 and April 2017, covering both enterprises identified at

baseline and newly established enterprises. This served as the endline survey sampling

frame; we randomly sampled up to 5 enterprises per village, stratified by those operating

from within and outside of homesteads. Surveys covered revenue, profits, employees, wages,

some other costs, and taxes paid. The main endline sample includes 1,699 enterprises oper-

ated from within and 1,442 from outside the homestead (both from enterprise surveys), as

well as 7,899 agricultural enterprises from the household survey. Enterprise characteristics

appear balanced across treatment and control villages at baseline (Table D.3): there are

no statistically significant differences at the 5% level, and two of 18 are significant at 10%,

which we would expect by chance.

This integrated approach to household and enterprise surveying allows us to match firms

to their owners. We match all agricultural enterprises (as found via household surveys), and

56% of non-agricultural enterprises, for a total of 93% of all enterprises. Based on this match,

we estimate that enterprise activity is highly localized, with 92% of total profits and 87% of

revenues accruing to owners who live within the village in which the enterprise operates.

20. This is calculated as se,c´

řRr“2

´

β1r ` β

2r

¯

˚`

ĘAmtv,r|i is an eligible non-recipient˘

¯

`

si´

řRr“2 β

1r ˚

`

ĘAmtv,r|i is ineligible˘

¯

, where se,c “ 1 ´ si is the population share of eligible non-

recipient village households among all non-recipient households, and the β1r and β2

r terms come fromEquation (3).

12

3.5 Empirics: enterprises

We estimate enterprise-level effects using versions of Equations (1) and (2), with radii bands

selected as above, interacting right hand side variables with enterprise type (Appendix D.2

lists the full specifications). We include village-level means rather than enterprise-level val-

ues of the lagged dependent variable given that the enterprise surveys were repeated cross-

sections. We carry out estimation using inverse probability weighting, accounting for enter-

prise type, except in some cases where we also revenue-weight outcomes. As above, we calcu-

late and report average total effects, weighting effects for the three enterprise types, namely,

agricultural enterprises, non-farm enterprises operating within homesteads, and non-farm

enterprises operating outside the home; we typically pool data across all enterprise types,

except when we do not observe some outcomes for agricultural enterprises. To facilitate

comparisons between the household and enterprise results, we also normalize effects as per-

household rather than per-enterprise.21 To examine extensive margin effects, we estimate

village-level analogues to this approach with the total number of enterprises censused (per

household) as the dependent variable.

3.6 Price data

We measure consumer goods prices using monthly surveys of commodity prices in local

markets. These surveys were conducted over the course of 2 to 2.5 years in all 61 markets in

the study area (and neighboring towns) with at least a weekly market day, for a total of 1,586

market-by-month observations and 311,138 non-missing price observations. We have market

price data prior to the disbursement of any local cash transfers for all markets, providing an

appropriate baseline for the panel data econometric analysis detailed below, and allowing

for the inclusion of market fixed effects. These include market centers located in towns,

and so will appropriately reflect the impacts of households (potentially) traveling to towns

to spend their transfers. Figure A.2 shows the substantial variation in treatment intensity

around markets, as well as the heterogeneity in village proximity to markets. The average

village had 0.7 markets located within 2 km and 2.3 markets within 4 km, again indicating

the rather high density of settlement. Household respondents report an average commuting

time to their preferred market of 33 minutes, where over 75% walk to the market.22

21. Specifically, we calculate 1nhh

ř

gx∆y

g

e ˚ ngent, where nhh is the total number of households across all

control villages (column 2) or treated villages (column 3), x∆yg

e is the estimated average effect (β ˚ X) forenterprise type g, and ngent is the number of enterprises of type g in the control or treated villages.

22. Enterprises in markets account for 65% of non-agricultural enterprise revenue, based on a 2019 censusof enterprises. We did not collect price data as comprehensively from the minority of enterprises locatedoutside of markets and dispersed within villages, both for logistical reasons and because their products tendto be less standardized. That said, estimated impacts on the prices of two common services these enterprises

13

Market surveys collected prices for 70 relatively homogeneous products, including food

(grains, vegetables, fruit, meat), livestock (goats, sheep), hardware (nails, paint), “duka”

kiosk store products (non-food and packaged food), and others (e.g., fuel, health items,

household items, and farming implements). We collected quotes from three vendors of each

product in each market in each month, and use the median for each product-market-month.

We then calculate linear log-price indices by weighting prices by household expenditure

shares.23 We also examine effects on subcategories of goods, which include: food items; non-

food non-durables (such as soap, cooking fat, and firewood); durables (such as iron sheets

and jerry cans used for transporting water or fuel); livestock; and temptation goods.24

We measure prices of the major factors of production using household survey data on

wages, land prices, and interest rates on formal and informal borrowing and lending. Because

compositional changes in these inputs may be important, we examine quantity and price

effects side by side.

3.7 Empirics: prices

We estimate effects on consumer goods prices using both spatial and temporal variation

in the amount of cash distributed around each market. In contrast to the household and

enterprise data, our repeated measurement of prices, both before and after the start of cash

distributions, allows us to estimate equations that include market fixed effects.These absorb

any systematic price differences across markets as well as differences in the share of eligi-

ble households located around those markets, conditional on which treatment is randomly

allocated so that we do not need to instrument for treatment amounts in each buffer. In

Appendix E.2.3, we demonstrate robustness to using an IV approach analogous to that used

with household and enterprise data. Specifically, we estimate

pmt “Rÿ

r“2

Mÿ

l“0

βrlAmtmpt´lq,r ` αm ` λt ` εmt (4)

where pmt is a price outcome for market m in month t. Amtmpt´lq,r is the per-household

amount transferred within band r´2 to r km around market m in month t´l, expressed as a

offer, tailoring and maize grinding, are if anything smaller than estimated effects on our main market priceindex (Table E.5).

23. We use expenditure data from the the Kenya Life Panel Survey (Baird et al. 2016) conducted in 2013-2014 in rural areas of Siaya and neighboring Busia county. We use the KLPS data because we did not collecta full expenditure module at baseline (due to project time and budget constraints) and prefer not to useendline expenditure data which are potentially endogenous. That said, results are nearly unchanged if weuse consumption expenditure shares from non-recipient households in our endline survey.

24. The consumption expenditure measure of temptation goods includes alcohol, tobacco, and gambling.The price index includes the cost of cigarettes.

14

fraction of GDP. We exploit our panel setup by conditioning on fixed effects for both markets

(αm) and months (λt). The latter account for seasonal differences and other time trends

common to all markets. We again account for spatial correlation in calculating standard

errors (Conley 2008). We determine both the relevant spatial distance R and the relevant

temporal lag M over which price effects persist by minimizing an information criterion

conceptually similar to that above, but adapted to account for the fact that the BIC cannot

select between non-nested models (such as one with a high R and another with a high M).

Specifically, and as pre-specified (Appendix I), we first select R while holding M fixed at 3

months by estimating models of the form

pmt “Rÿ

r“2

βr`

Amtmt,r ` Amtmpt´1q,r ` Amtmpt´2q,r

˘

` αm ` λt ` εmt (5)

where R varies between 2 km and 20 km. We select the value R “ R that minimizes the

Schwarz BIC while imposing weak monotonicity. We then select the number of monthly

lags M by estimating Equation (4) with R “ R and choosing the model that minimizes

the Schwarz BIC. This procedure selects only the 0-2 km band (and sometimes the 2-4

km band) around each market and a single temporal effect, implying that we only include

contemporaneous transfers in estimating price effects. Appendix E.2 presents results for a

specification where we impose R = 4 km and M = 18 months for robustness, and yields

similar results.

Identification in Equation (4) comes from the roll-out of treatment across space and time,

and the project’s research design leads to substantial variation in both dimensions. As noted

above, there is considerable variation in the total amounts of cash going to the 0–2 km ring

around each market. Moreover, the multi-year nature of the market data covers periods

both of intensive transfer distribution as well as times when no transfers were going out. As

above, we are unable to capture price increases that radiate throughout the whole study area

(compared to neighboring counties) over the entire period, but the highly localized nature

of the price effects that we do detect suggests that any such effects are unlikely to be large.

We use estimates of Equation (4) to calculate two price effects. The implied average

treatment effect (ATE) is the average price effect across all markets and all months in which

any transfers went out to any market in the study area, i.e., during the study period of

September 2014 to March 2017. This is simply equal to the estimated coefficients multiplied

by the mean of the corresponding regressors of interest. The average maximum transfer effect

is the average across markets of the estimated effect in the month in which the maximum

amount of cash (as a share of GDP) was distributed into the selected radii bands (in other

words, out to R) from the market.

15

We focus on two sources of heterogeneous price effects. First, we classify goods into

those that are more and less tradable, where the former include relatively easily transported,

non-perishable items, and the latter include more difficult to transport or perishable items.25

Second, we classify markets into those with better or worse market access. Standard theory in

international trade predicts that more integrated markets should be less likely to experience

meaningful price changes following a local aggregate demand shock. We examine output

price heterogeneity with respect to a commonly used metric of market access26 (MAm)

MAm “ÿ

d

τ´θmdNd «

10ÿ

r“1

r´θNr (6)

Geographic distance r is used to proxy for trade costs between origin market m and des-

tination d, i.e., τmd “ r. Destinations are 1 km radii bands around each market, with

total population Nr in each buffer, and we follow Donaldson and Hornbeck (2016) in setting

θ “ 8. Within quantiles of this metric, we calculate average and average maximum transfer

treatment effects in the manner described above.27

We estimate effects on input prices using Equations (1), (2), and (3), as our input price

data come from household surveys, and report the corresponding average treatment effects.

3.8 Empirics: dynamics

To estimate the multiplier, we extend the cross-sectional analysis by estimating and then

integrating effects on components of GDP over time.28 For a flow variable x (e.g., con-

sumption, investment, etc.), we first estimate the following specification, which is a dynamic

extension of previous estimating equations:

xit,v “ αt `9ÿ

s“0

βsAmtvpt´sq `9ÿ

s“0

γsAmt vvpt´sq,0-2km ` εit,v. (7)

25. For instance, more tradable goods include building materials (e.g., timber, cement, nails, iron sheets)and some household goods (soap, firewood, charcoal, batteries, washing powder), while less tradable goodsinclude some food items (e.g., avocado, banana, cabbage, egg, pork, fish) and livestock. These classificationswere undertaken based on feedback from Kenyan project staff, but there may, of course, be some ambiguityabout specific items. The full pre-specified classification is in Appendix E.

26. Absent data on trade costs, we have to make an assumption about the elasticity of trade costs withrespect to distance. We set the elasticity equal to 1 and conclusions are robust to alternative assumptions.

27. We also consider an alternative market access metric, namely, road access, defined as the inverse distancefrom the closest main road (as captured by Open Street Map), see Appendix E.2.2.

28. We stated our intention to estimate a multiplier in our pre-analysis plans but did not fully specify theeconometric approach for doing so.

16

where Amtvpt´sq is the amount transferred to village v in quarter t ´ s, instrumented by a

treatment indicator Treatv multiplied by the share of total transfers going to village v in

quarter t ´ s, and analogously Amt vvpt´sq,0-2km by the share se,t, vv,0-2km of eligible households in

the 0 to 2 km buffer around v (but not in village v) assigned to treatment multiplied by

the share of transfers going to that group in quarter t ´ s. The coefficients in this model

are identified by the fact that village treatment status was randomized, and the timing of

both cash transfers and survey data collection was rolled out to villages in a randomized

order. The main challenge is that the first household surveys started around 9 months after

the experimental start date in each village, while enterprise surveys began after about 18

months (see Figure A.1). With a few exceptions, recall periods are less than or equal to

one month, so we often do not directly observe the initial response in flow variables in the

months immediately after the first transfers went out, which is when we might expect to see

some of the largest impacts on expenditure. Given that the specification treats each dollar

transferred symmetrically, we can still estimate the local response during these early quarters

because transfers to recipients rolled out over 8 months. Similarly, we estimate neighborhood

effects using the substantial variation in the timing with which nearby villages were treated.

However, we tend to obtain less precise estimates of responses in early quarters as they are

estimated using less variation in treatment intensity compared to later quarters.

We then integrate dynamic effects on flow variables over time up to 29 months (10 quar-

ters) after treatment. We compute the dynamic profile of treatment effects (or the impulse

response function, IRF) using the coefficients estimated above and assuming that the treat-

ment rolled out to recipient households as planned: the timing is a token transfer at time 0,

a first lump-sum 2 months later, and a second 8 months after the token transfer. We com-

pute this IRF separately for recipient and non-recipient households, and separately for the

three categories of enterprise in both treatment and control villages. We then aggregate the

quarterly estimates across all villages (using inverse population weights from our household

and enterprise census) to compute the study area-wide IRF for each flow component.

We conduct inference on the multiplier estimates this procedure yields using the wild

bootstrap clustered by sublocation, the highest unit of randomization (Cameron, Gelbach,

and Miller 2008).29 We focus on two one-sided hypotheses, namely, that the multiplier is

less than zero and that it is less than one. We test these hypotheses using our income- and

consumption-based multiplier estimates separately, as well as using the average of the two.

29. While this procedure may perform poorly in cases where most units in treated clusters are treated andthere are few clusters, here at most two thirds of households in the most intensely treated clusters weretreated, and there are 84 clusters, far above the 15-20 that MacKinnon and Webb (2018) deem adequate.

17

4 Tracing out the path of spending

We now turn to tracing out the path of spending induced by the cash transfer experimental

intervention. We start by documenting effects for recipient households, then for enterprises

and untreated households. Monetary units are USD PPP unless otherwise defined (where the

transfer was worth USD 1,871 PPP), flow outcomes are annualized, and monetary outcomes

are top-coded at the 99th percentile (as pre-specified), unless otherwise noted.30

4.1 Recipient household effects

The main household expenditure measure is the (annualized) sum of total food consumption

in last 7 days, frequent purchases in the last month, and infrequent purchases over the last 12

months.31 Durables expenditures are the sum of home maintenance, home improvement, and

other household durables spending, and the remainder classified as non-durable spending.

As expected, recipient households report significantly higher total expenditure: USD

PPP 293 more expenditure than eligible households in control villages (Table 1, column 1),

an 11.5% increase over the control village in low saturation area mean of USD PPP 2,537.

The estimated total treatment effect, including spatial effects, is larger at USD PPP 338, a

13.3% increase (column 2). This pattern between columns 1 and 2 is a first piece of evidence

for localized, positive cross-village spillovers, which is repeated across other outcomes.

The pattern of expenditure effects by category is broadly consistent with earlier work

(Haushofer and Shapiro 2016). Both non-durable and durable spending increase substan-

tially. Food expenditure accounts for a sizable portion of the increase in non-durable expen-

diture in both columns (38% and 59%, respectively). We can reject meaningful increases in

reported spending on temptation goods, consistent with Evans and Popova (2017).32

Consistent with increased expenditure on durables, asset stocks also increase (Table 1,

Panel B). Anecdotally, many recipients withdrew money from M-Pesa immediately and saved

via durable assets. The main pre-specified measure of assets includes livestock; transporta-

30. The main measures were pre-specified, though some groupings vary from the PAP to ease exposition.31. The survey was quite comprehensive. In addition to food consumption, frequent purchases include

airtime and other phone expenses; internet; transport expenses (including petrol); lottery tickets and gam-bling; clothing and shoes; recreation and entertainment; personal toiletry and grooming; household items,such as cleaning products and candles; firewood, charcoal and kerosene; electricity; and water. Infrequentpurchases include house rent/mortgage; home maintenance; home improvements; religious expenses; educa-tion expenses; charitable donations; weddings and funerals; medical expenses; household durables, includingfurniture, lamps, cutlery, pots and pans and other kitchen equipment; and dowry or bride price.

32. While there is likely some under-reporting of temptation goods, the fact that the control group meanis non-trivial demonstrates that at least some households feel comfortable reporting such spending. Givenour limited expenditure data immediately after transfer receipt, we cannot rule out that temptation goodspending increased temporarily at that time.

18

tion (bicycles, motorcycles, and cars); electronics; farm tools; furniture; and other home

goods; we add in net household lending to, and borrowing from, both formal and informal

sources. This measure of assets increases by USD PPP 182, or 25% of the mean for eligible

households in control villages in low saturation sublocations.33 This measure excludes the

values of housing and land, which are harder to measure given thin local markets, but also

likely important given existing work shows that households often use GD transfers to spend

on housing materials (Haushofer and Shapiro 2016). We separately measure housing value as

the respondent’s self-reported cost to build a home like theirs, and land value as landholdings

multiplied by the household’s report of the per-acre cost of land of similar quality (in their

village). Estimated housing value increases by USD PPP 481, or 79% of the control mean,

and estimated land value increases, though this effect is not statistically significant.

Theoretically, the effect of a large-scale wealth transfer on earnings is ambiguous: it may

reduce labor supply through an income effect, but may also enable productive investment or

increase labor demand. In the data, recipient households’ income from all sources (excluding

the GD transfers) does not appear to have decreased: point estimates are positive (USD

PPP 78 and 134 in the two main specifications) and the reduced form effect is marginally

significant.34 For labor supply specifically, we do not find that recipient households worked

less; if anything, total hours worked by recipient households in agriculture, self-employment

and employment increased slightly though not significantly (Table 2, Panel A, columns 1 and

2). This is consistent with the studies reviewed by Banerjee et al. (2017), which generally

find that cash transfers in low and middle income countries do not reduce labor supply.

Interestingly, we observe little heterogeneity in estimated treatment effects (on assets,

expenditure, income, and hours worked) among eligible households across eight pre-specified

characteristics (Figure A.4), namely, respondent gender, age over 25, marital status, primary

school completion, having a child in the household, an indicator for above median measured

psychological well-being, and work status (in self-employment or wage employment).

The effect on net transfers received from other households is also notable: the point

estimate is negative but not statistically significant, and we can reject large changes in

either direction. This suggests that relatively little of the cash transfer was literally shared

with neighbors or social contacts.

33. The mean for eligible households in control villages and low saturation sublocations is USD PPP 724(with SD 863), less than the overall mean, unsurprisingly since ineligible households are wealthier.

34. As is common in low-income settings, measured values of consumption are larger than measured house-hold income. Similarly, total measured local area income and firm revenue is lower than expenditures, inpart, because measured expenditure includes important categories – including medical and schooling ex-penses, utilities, rent and mortgage, religious and charitable donations, and dowry, wedding and funeralcosts – for which we do not typically measure corresponding revenues in the enterprise data. Expendituremeasures may also better capture consumption of own-farm production than the agricultural revenue data.

19

Overall, these results highlight that cash transfer recipients substantially increased their

expenditure on a broad range of goods. This spending was likely financed primarily by the

initial transfers themselves, with possibly some contribution from higher earnings. A large

share of this spending likely takes place locally: enterprises report that 86 percent of their

customers come from within the same village or sublocation. Below we therefore turn to

examining impacts on local enterprises.

4.2 Estimating the Marginal Propensity to Consume

The marginal propensity to consume (MPC) sheds light on the inter-temporal decision-

making of households, and is an important determinant of the magnitude of a transfer

multiplier, as it captures the share of income that is spent—and thus enters the hands of

other agents in the economy—rather than being allocated to financial savings or retained in

cash (which in our setting might include simply retaining some value on the mobile money

platform). The dataset allows us to generate an intuitive estimate of the MPC out of the

transfer, obtained conceptually by dividing the total increase in expenditure by the size of

the GiveDirectly transfer.35

Here we summarize the construction of the MPC in our data; refer to Appendix G for

details. An immediate cross-sectional estimate can be obtained by dividing the effect on

total household non-durable consumption in Table 1 by the size of the transfer among re-

cipient households. However, this underestimates the MPC, as it is based on consumption

as captured in the period preceding household survey administration, with a retrospective

timeframe of at most 12 months, compared to the full transfer value, which for many house-

holds was distributed at least in part more than 12 months ago. It misses any changes to

consumption occurring outside this window, particularly in early months when spending may

be the highest. We can improve on this by employing the dynamic regression specification

(in equation (7)), which exploits the fact that the timing of survey data collection, relative

to transfer disbursement, varied exogenously across households.

Yet this estimate is also a lower bound. As noted above, a limitation of the data collection

is the relative lack of household survey data collection in the months after transfers went out,

the period when, anecdotally, a large share of the transfer was spent. We thus augment the

analysis by making use of data collected as part of the closely related Haushofer and Shapiro

(2016) study of GiveDirectly transfers provided between 2011–2013 in a nearby part of Siaya

35. This measure is comparable to MPC estimates from tax rebates (e.g., Parker et al. 2013). Alternatively,it may be attractive to divide by the transfer size plus any additional non-transfer income generated overthe period. Table 1 shows that this increase is small and not significant, with a point estimate of « 7% ofthe transfer value. Thus results do not change substantively if this additional recipient income is included,although its inclusion does reduce the estimated MPC somewhat, see Appendix Table G.1

20

County (Rarieda subcounty, lying just outside our study area), which gathered information

on household consumption immediately after transfers. The MPC of non-durable goods

among recipients in the first three quarters following the transfer there was 0.35 (Appendix

Table G.1), consistent with much spending occurring shortly after transfer receipt. Combined

with estimates from our data thereafter, recipients’ MPC on non-durables over the 27 months

post-transfer is 0.64. This implies that most study households receiving cash transfers were

hand-to-mouth consumers, allowing us to soundly reject the permanent income hypothesis

in our context.

This estimate still leaves out durable goods expenditure. First note that households re-

port purchasing the vast majority of durables (over 95%) in local shops. These durables may

serve as consumption, savings or investment goods. A large share of such purchases in the

study sample are consumer durables not primarily intended for productive uses (e.g., radios,

furniture). At the same time, formal sector financial savings are limited in rural African

settings like ours and much household saving comes in the form of purchases of household

durable assets, which necessitates spending on local goods. Thus from the perspective of

inter-temporal decision-making, durables are more of a gray area. Yet whether durables are

purchased as “savings goods” or “consumption goods”, both types of expenditure show up

as revenue of local firms and may therefore have similar stimulus effects. Here we rely on the

cross-sectional difference in the value of durable assets (including housing) between treat-

ment and control areas among eligible households in our endline data (Table 1). Combining

this non-durable expenditure yields our best estimate of the overall MPC in the 27 months

following transfers, at 0.93.

Because we are interested in estimating the multiplier effect on local economic activity

(within the study area), we next refine the MPC estimate by focusing on spending on lo-

cal value added, excluding spending on intermediates and final goods produced elsewhere.

Spending on goods produced in other parts of Kenya (or the world) does not directly con-

tribute to local GDP (although it could generate multiplier effects at larger geographic scales

that we cannot readily assess with our data). We thus derive a bound on the share of spend-

ing on local value added. This is closely related to the local degree of openness that features

prominently in discussions such as Farhi and Werning (2016). We find that most consump-

tion is in fact of locally produced goods, in line with the well-known fact that a large share

of household consumption in rural areas consists of locally produced food and other basic

necessities (Deaton 2018). In particular, the enterprise data allows us to bound the share

of imported intermediate goods sold in the study area, where, recall, over 95% of household

shopping occurs.36 This conservative methodology yields an upper bound of 18% for the

36. As discussed in Appendix H.1, we determine that at most a fraction 1´ costi`profitirevenuei

of the revenue of

21

expenditure-weighted share of local non-durable expenditure (and 20% for durables) that

may reflect expenditure on imported intermediates, indicating that four fifths of spending is

on local value added, and thus that the study area’s economy is largely closed.37

Combining estimated import shares with our preferred MPC estimate yields a marginal

propensity to consume on local value added, which we denote MPCLocal, of approximately

0.76 in this context. Of course, this figure is subject to the data and measurement caveats

noted above, as well as assumptions on the share of imports, and so should be seen as

speculative. Nonetheless, taking this value of 0.76 to a basic static Keynesian model, the

transfer multiplier effect on local output would be MPCLocal1´MPCLocal

« 3.2. We dynamically estimate

the multiplier using all household, enterprise and price data in section 5 below.

4.3 Enterprise effects

There are large increases in revenue for enterprises in both treatment and control villages

(Table 3, Panel A). Revenues in treated villages increased by USD PPP 357 per household, a

47% increase, while those in control villages increased by USD PPP 244 (32%). Revenue gains

are concentrated in the retail and manufacturing sectors: both treatment and control villages

experience statistically significant increases in manufacturing revenue of similar magnitudes

– USD PPP 109 and 110, respectively – while treatment villages see larger gains in retail

revenue (USD PPP 141 versus USD PPP 65, Appendix Table A.2).

Estimated effects on profits are positive, but moderate in magnitude and not significantly

different from zero. In fact, profit margins (measured as the ratio of profit to revenues) fell

(Table 3, Panel A, Row 5). We also see no evidence of firm entry, as one might have expected

if enterprises were becoming more profitable (Panel C). Overall, the data indicate that higher

revenues were largely absorbed by increased payments to various factors of production. While

we do not observe all of these payments, we do see significant increases in the factors that

we directly measure, and particularly the wage bill: enterprises in treated (control) villages

increase spending on labor by USD PPP 82 (71), a sizable change relative to the mean.

Strikingly, we do not see strong evidence of a firm investment response. Estimated

increases in fixed capital investment are small, and we can reject large changes (Panel B,

firm i is spent on intermediate goods; for each firm type, we then generate a revenue-weighted average upperbound for the share of intermediates in its production function. Next, we make assumptions about whatshare of intermediate goods is likely imported, conservatively erring on the side of assuming a high share;for instance, we assume that all intermediate goods at clothing stores (which spend up to 38% of revenue onintermediate goods) are imported, which is likely to be an upper bound.

37. In principle this exercise also depends on migration: money spent elsewhere by migrants appears inour data (as we tracked and surveyed them) but does not contribute towards the share spent on localvalue added. In practice household migration was uncommon, with 5% of control low-saturation householdmigrating, and unaffected by treatment (Table A.9, Row 1). Estimated treatment effects among non-migrantsare also essentially identical to overall average effects (Table A.9, Panel 2).

22

Row 2). We do see a modest increase of USD PPP 35 in inventories for enterprises located in

treated villages, yet even this appears to be less than proportional to the increase in firm sales;

in other words, these enterprises are, if anything, operating leaner business models (Panel B,

Row 1). This pattern of results suggests that the expansion in enterprise activity is driven

more by the shock to local aggregate demand than by a relaxation of credit constraints that

had previously limited investment.

One caveat to this point is that some household assets are difficult to categorize into

“productive” assets as opposed to consumer durables. For example, bicycles may be used

for personal transportation (i.e., to visit friends), but could also be used as a bicycle taxi

to generate income. We therefore inclusively categorize as “potentially productive” both

livestock as well as a number of non-agricultural assets that could potentially be used for

income-generating activities (beyond simply renting out the asset).38 When we do so, overall

roughly half of the increase in household asset ownership documented above is in what we

believe to be purely non-productive assets, with small gains in productive agricultural assets

(e.g., farm tools) and a modest gain for potentially productive assets (Table A.1). We also

fail to detect any investment response for non-agricultural enterprises owned by recipient

households: neither investment nor inventories increase relative to eligible owners in control

villages (Table A.3, Panel B). Taken together, these patterns are also consistent with the

cash transfer program generating only a limited local investment response.

4.4 Non-recipient household effects

There are positive and significant expenditure effects for non-recipient households. Column

3 of Table 1, Panel A presents results based on Equation (3). Notably, the magnitude of

these gains (USD PPP 334, p-value ă 0.01) are quite similar to those of recipient households

(USD PPP 338). The pattern of expenditure increases is also broadly similar to that for

recipient households, except that spending on durables does not increase among non-recipient

households. One possible reason for the similarity in overall spending impacts is that the

timing of effects on recipient and non-recipient households may be different, with recipient

households showing impacts earlier than non-recipient households, but effects converging by

roughly one year after the final transfer was received. A further potential mechanism is that

labor earnings increase differentially: among non-recipients, annual labor income increases by

USD 229, while the figure is USD 134 for recipients. For wage earnings, the figures are USD

183 and USD 73, respectively. Thus, the similar impacts on expenditure among recipient and

38. Potentially productive non-agricultural assets include bicycles, motorcycles, cars, boats, kerosene stoves,sewing machines, electric irons, computers, mobile phones, car batteries, solar panels or systems, and gen-erators. Examples of residual non-productive assets include radio/CD players, kerosene lanterns, beds,mattresses, bednets, tables, sofas, chairs, cupboards, clocks, televisions, and iron sheets.

23

non-recipient households may partly be explained by a lower labor income response among

the former. Finally, note that non-recipient households include both eligibles and ineligibles,

and, as shown in Table A.8, most of the gains accrue to ineligibles. These comparatively

wealthier households might be gaining more from business and additional labor income, and

may be imperfectly substitutable with eligibles in the labor market. As a result, they may

experience a larger increase in wages than recipient and non-recipient eligibles.

How did non-recipients fund these consumption gains? One possibility is that they are

dis-saving, perhaps due to social pressure to “keep up with the Joneses”, their neighbors who

received the transfer. However, this does not appear to be the case: estimated treatment

estimates for total assets, housing and land values are all positive, although not all are signifi-

cant (Table 1, Panel B). Nor do we observe a borrowing response for non-recipient households

from either formal and informal sources (Table 2, Panel C, column 3). A second potential

explanation is that expenditure gains reflect inter-household transfers to non-recipient house-

holds, as documented in Angelucci and De Giorgi (2009) for Mexico. This also does not seem

to be the case, as we find no significant increase in net transfers received by non-recipient

households, and the point estimate of USD PPP 8.75 is less than 3 percent of the expenditure

gain for non-recipient households; this mirrors the lack of an effect on net transfers among

recipient households noted earlier.

Rather, the data suggest that consumption gains are driven by higher earned income:

total annualized income increases by USD PPP 229. It is often argued in development

economics that survey estimates of consumption are better measured and often substantially

larger than estimates of income, particularly for poor households (Deaton 2018). While this

is true in our case, we cannot reject that the total effect on income is the same as the

effect on consumption expenditure for non-recipient households (p = 0.23). Income gains

come largely from wage earnings, which increase by USD PPP 183, with a smaller and not

significant contribution from profits from owned enterprises. These results are broadly in line

with the enterprise results, in which profit increases were modest and marginally significant

while the wage bill expanded significantly, by 68 and 58% in treatment and control villages,

respectively (Table 3, row 4). Higher wage earnings appear more likely to reflect higher

wages than increased labor supply, as the point estimate for overall household labor supply

is actually somewhat negative (although there does appear to be an increase in respondent

hours worked for wages, Table A.4). Hourly wages earned by non-recipient household increase

meaningfully, although the estimate is only marginally significant (Table 2, Panel A).

To sum up the results so far, cash transfer recipient households receive and spend most

of the transfer, leading to higher local enterprise revenues. This positive aggregate demand

shock, in turn, appears to increase the income of local non-recipient households, leading to

24

higher spending on their part. This pattern provides initial evidence for a positive multiplier

effect of the cash transfer program, an issue we return to below.

4.5 Effects on output prices

We turn next to effects on consumer goods prices in order to understand the extent to which

other monetary impacts are real as opposed to nominal. Overall, we find small, positive and

precisely estimated effects on consumer goods prices. For our overall expenditure-weighed

log-index of market prices both the ATE and average maximum transfer effect are small and

precisely estimated near zero (Table 4). The tight standard errors allow us to rule out even

relatively small price effects: with 95 percent confidence, the ATE across the study period

is below 0.0022 log points, or 0.22 percent. For the average maximum transfer effect across

markets, the upper bound of the 95 percent confidence interval is 0.01 log points, or 1 percent.

Price effects are also small across almost all product categories. In particular, food prices

are in line with the overall price index, and durable prices do not increase meaningfully. To

help mitigate concerns that results may be sensitive to the price index weights or product

classification, we find that average price inflation is below 1.2% for every product (Figure

A.6; for alternative specifications and product classifications, see Appendix E.2).

Variation in price responses is generally in line with theoretical predictions. We observe

somewhat larger price increases in markets less integrated into the local economy. Columns 3

and 4 split markets into those above and below median market access, with estimated effects

typically more positive in more remote markets. Figure A.5 further breaks this pattern down

by quartile of market access, with lower values reflecting more isolated markets. Panels A-C

show a small amount of inflation for less tradable goods only in the most isolated markets,

and smaller and less precisely estimated effects for more tradable goods, with less of a clear

pattern across market access quartiles. Inflation for less tradable goods in isolated markets

nonetheless remains limited, at 0.2-0.3% on average. We also carried out enterprise phone

surveys of a subset of enterprise types during the period in which transfers were going

out, which collected price data on a limited number of products; inflation for these local

manufacturing and services prices is also limited (see Appendix E.3).

These patterns are qualitatively similar to findings in Cunha, De Giorgi, and Jayachan-

dran (2018), who study the price effects of an in-kind food and cash transfer program in

Mexico (where the household income shock was similar in magnitude to the Kenya program

we study): in-kind transfers there lead to price decreases, while cash transfers lead to price

increases, but their estimated effects are small except in remote villages. Filmer et al. (2018)

estimate inflation of 5 to 7% for protein-rich foods in the Philippines, with smaller effect

for other product categories. Burke, Bergquist, and Miguel (2019) show that a credit inter-

25

vention impacting the supply of staples also affects local grain market prices in a different

Kenyan region. Reconciling these results with ours is a task for future research.

4.6 Effects on input prices

We next examine effects on the prices of major factors of production: labor, land and capital.

Table 2 presents estimated effects on these prices measured in the household survey data.

We find some evidence of higher wages. In row 1 of Table 2, we examine wages for employees

using household survey data.39 In the reduced form specification, eligible households in

treatment villages earn USD PPP 0.11 more per hour, on a base of USD PPP 0.70. This

effect is no longer significant, however, when we also estimate across-village spillovers. For

non-recipient households, the increase is even more marked at 0.19 USD PPP per hour, and

significant at the 10% level. These potentially large wage effects do not seem to be driven

by large labor supply responses. In row 2, we calculate the total hours worked by adult

household members in agriculture, self-employment and employment, and estimate effects

at the household level. Effects are relatively small and not significant. Together with the

fact that enterprise wage bills increased, these patterns are strongly suggestive of positive

local wage effects (Table 3). This in turn suggests that labor markets in this area are fairly

localized, at least over the time horizon we study, which is consistent with the fact that we

see little evidence of impacts on measures of migration (Table A.9). In the longer run, labor

may become more mobile, helping to equilibrate any induced wage differentials.

Effects on estimated land prices are positive and economically meaningful (at 9-14%),

but not significant (Table 2, Panel B). Since our measure of land prices is a somewhat noisy

one—formal sales are rare so we use respondents’ self-reports of the amount per acre land like

theirs in the same village would sell for—we also examine land rental prices as a robustness

check, which yields data on actual land transactions for a subset of respondents. We do not

find significant effects on land rental prices (Table A.5). Unsurprisingly, given land should be

in relatively fixed supply in the short-run, we find little change in total landholdings among

recipient households or those in more heavily treated areas. We also find no effects on total

land rentals, nor on the total amount of land used for agriculture (Table A.5).

We estimate fairly precise null effects on interest rates and total borrowing (Table 2,

Panel C), where we measure household borrowing from both formal (e.g., banks, mobile

credit services) and informal (moneylenders, family and friends) sources. The loan amount

reports total borrowing across sources in the last 12 months, setting those who did not

borrow equal to zero. Note that the loan-weighted interest rate is the monthly interest rate

39. We include all household members that report working for wages, and calculate their hourly wage basedon hours worked in the last 7 days and their monthly salary (adjusted to weekly scale).

26

on the most recent loan by source, weighted by the total amount of borrowing (by source);

we include informal loans without interest, which brings down the average rate.

5 The transfer multiplier

We next examine what the household and enterprise responses imply for the aggregate level

of economic activity, and specifically for the value of the local multiplier of cash transfers,

where ‘local’ refers to the entire study area. We define this multiplier M as the cumulative

effect of transfers on local real GDP, relative to the total amount T transferred in real terms,

over a given time interval:

M “1

T

˜

ż t“t

t“0

∆GDPt

¸

(8)

The size of the transfer multiplier is generally thought to depend in part on the policy

context in which outlays are made, and in particular on the extent to which (i) monetary

policy reacts, and/or (ii) households and firms expect levels of current or future taxation

to change. Our setting is unusual in a useful way: because we observe a large one-time

fiscal outlay that was made philanthropically, funded from outside of the economy we study,

and small relative to the overall Kenyan economy, we can reasonably expect to measure a

“pure” external transfer multiplier that should be independent of such effects. This feature

generates estimates that can be thought of as a model primitive, and with which estimates

from other financing scenarios can be contrasted.

As noted in Section 4.2, an initial calculation of the transfer multiplier as MPCLocal1´MPCLocal

suggests that it may be substantial, at around 3.2. In this section, we refine this estimate by

both accounting as fully as possible for effects on all components of GDP, including spillover

effects, and accounting for dynamics. To get at real values, we deflate all monetary outcomes

and transfer values to January 2015, linking the overall monthly market price index in the

nearest market to each observation (Appendix H presents a nominal version).

Following national accounts definitions, the expenditure-based measure of local GDP is

GDPt “ Ct ` It ` Gt ` NXt, where Ct is consumption expenditure on non-durables and

durables, measured as quarterly consumption plus accumulated assets and housing stock at

endline.40 To avoid potential double-counting, we exclude expenditure on home durables,

home improvements and maintenance from the consumption expenditure measure as part

of this expenditure may be reflected in an accumulation of assets. In addition, we exclude

net lending as well as land values from the asset measure because changes in land values

40. Note that by measuring impacts on asset stocks we (correctly) do not count transfers of existing assetsbetween local agents as GDP, since these increase one agent’s balance sheet while decreasing another’s. Suchtransactions only introduce bias if they involve a non-local counterparty, as discussed below.

27

may not be driven purely by investment, and because we think of land supply as being

essentially fixed. We exclude local government expenditure, Gt, as Walker (2018) shows that

the intervention had a precisely estimated null effect on it.

Since we also measure household and enterprise income, we can construct a dual income-

based measure of local GDP as the sum of factor payments and profits: GDPt “ Wt `Rt `

Πt ` Taxt ´ NFIt, where Wt is the total household wage bill, Rt are rental expenses of

local enterprises (assuming those are paid to capital owners within our study area), Πt are

enterprise profits, and Taxt is total enterprise taxes.41

For flow variables, we follow Section 3.8 to generate IRFs, which we integrate over time.

For two components of GDP, we are instead able to measure impacts on the integral of flows

over time by simply measuring impacts on accumulated stocks, simplifying the problem.

Specifically, we measure effects on durable consumption expenditure using effects on the

stock of endline household durable goods and the value of respondents’ home, and effects

on inventory investment using effects on current inventory stocks at endline. One drawback

is that these figures are likely to under-estimate cumulative spending to the extent that

some assets depreciated between the time of purchase and measurement, although over the

limited timeframe considered this may be a second-order concern; any such bias would tend

to reduce the estimated multiplier. In the graphical presentation, we assume that any effects

on these stocks occurred equally across all post-treatment quarters.

Overall, we view the expenditure- and income-based multipliers as two distinct measures

of the same underlying concept, each with its own limitations. Reflecting this, below we

estimate them jointly and test individual as well as joint hypotheses across the two measures.

We discuss limitations and robustness in detail in Section 5.2, including adjustments to

account for the fact that we do not directly observe NXt or NFIt.

5.1 Multiplier estimates

We estimate a sizeable multiplier using both main approaches, in line with the back-of-

envelope figure derived above. The estimated expenditure multiplier is 2.53 (Table 5, Panel

A). 46% of this effect is driven by consumption expenditures. Household asset purchases and

enterprise investment make up another 32% and 19% respectively, and enterprise inventories

are not quantitatively important. While part of the asset response could potentially reflect

productive investments by household-operated enterprises, at least 43% of the asset response

41. We employ the household rather than enterprise wage bill, as the household survey sample is largerand includes individual-level wage earnings data. We omit land rental income because we do not see anysignificant evidence of effects on this above. In principle, a third approach to estimating GDP would beto aggregate value added from local enterprises; we do not implement this as we did not collect sufficientlycomprehensive data on enterprise expenditures on intermediate inputs.

28

comes from non-productive assets, across both recipient and non-recipient households (see

Table A.1). Taking this into account, consumption alone leads to an estimated multiplier

of at least 1.5, underscoring the overall point that cash transfers appear to have led to a

predominantly demand-side driven increase in local economic activity.

The estimated income-based multiplier is quite similar in magnitude to the expenditure-

based multiplier, at 2.28 (Panel B), and we cannot reject that they are the same (p “ 0.88).

This is notable since it is calculated using a completely distinct set of component measures.

Of this total effect, we find that 64% reflects increased enterprise profits, 30% increased

wages, and a much smaller contribution comes from capital income and taxes taken together.

As noted above, the increase in consumption, and the smaller increase in investment, is

therefore primarily accounted for by higher profits and wages. Of course, in our context of

predominantly single-person firms, “profits” likely reflect some mix of true economic profit

along with returns to the owner’s capital and labor inputs. Regardless of the exact mix,

however, this sum should be appropriate for our goal of calculating the aggregate income-

based multiplier.

When we examine the relative contributions of recipient and non-recipient households to

both multipliers (as shares of the total household contribution), we find that non-recipient

households account for 80% of the household contribution to the expenditure multiplier and

85% of the contribution to the income multiplier, both of which are somewhat higher than

their share in the local population of 67%. This suggests that analysis focusing only on

recipient households may be missing sizable shares of program effects.

An advantage of this “macro-experimental” approach to estimating the multiplier is the

ability to conduct statistical inference. To start, we reject the null of a negative multiplier

(with a value less than zero) at the 10% level using either approach (Figure 1 and Table

5), and reject the null at p “ 0.02 when testing the joint restriction, and at p “ 0.04 when

testing the average of both multipliers. Since the two measures exploit distinct data, we gain

statistical power by examining both measures together. Rejecting a negative multiplier on

real GDP is important, ruling out, for example, that prices adjusted immediately to increased

spending, netting out any real effects. Testing the null hypothesis of a multiplier less than

one has been a central goal of recent research on the fiscal multiplier, since it would imply

a crowd out of private spending, but this value does not have the same interpretation for

transfer multiplier estimates like ours where all spending is private. Nonetheless, rejecting

a transfer multiplier value less than one constitutes a conservative test for the existence of

positive output spillovers for non-recipients, holding even in the extreme case of MPC “ 1.42

42. A less conservative test of the no-spillovers hypothesis would be to test if the multiplier estimate is lessthan the MPC of recipients (which is strictly less than 1). Because this MPC is itself somewhat imprecisely

29

Using the expenditure or income-based approach alone, the p-value on this test is 0.14 and

0.23 respectively. The average of the two multipliers is 2.40 (SE “ 1.38, p “ 0.15), and

the hypothesis that the multipliers are jointly less than one is rejected at the marginally

significant p “ 0.07 level.

Figure 1 presents these results graphically, breaking up the aggregate multipliers into

quarters after transfers went out. Panel A presents the expenditure-based multiplier. The

increase in GDP is fairly stable over time; in fact, we cannot reject that the expenditure

response is constant across all quarters (p-value of 0.73). It increases slightly up to a peak

after 9 months (when the second lump-sum transfer has been received), and then slowly

declines. Interestingly, we reject a null effect as late as two years after the transfer, sug-

gesting that the true multiplier (out to an infinite time horizon) could be larger still and

that our estimates are likely to be lower bounds. The less precisely estimated effects (with

larger confidence intervals) during the first three quarters afters transfers go out are visually

apparent. The income multiplier, on the other hand, visually appears to fluctuate more over

time (Panel B): it is marked by a strong early response in profits, while wages appear to

take longer to rise. Yet as with the expenditure measure, we cannot reject equality of all

quarterly coefficients (p-value of 0.76).

These estimates are somewhat larger than the higher end of recent fiscal multiplier esti-

mates in the context of public spending in the United States (Chodorow-Reich 2019; Naka-

mura and Steinsson 2014), where they tend to range from 1.5 to 2.0. As noted above,

the magnitudes of transfer versus fiscal spending multipliers are not directly comparable.

The differences between our results and existing estimates may also reflect the relative lev-

els of economic development and other structural differences between the Kenyan and US

economies (such as the degree of openness of local economies, the share of hand-to-mouth

consumers and the existence of financial savings opportunities), differences in data and mea-

surement, as well as any effects on (or expectations of effects on) either monetary policy or

future taxes in the US, the latter being response effects that this study’s experimental design

usefully allows us to avoid.

5.2 Alternative assumptions

We also consider several alternative multiplier estimates that treat prices, exports/imports,

and the first three quarters of data post-transfer in different ways. A first alternative presents

the multiplier in nominal rather than real terms: the nominal expenditure (income) multiplier

is 2.66 (2.55), see Appendix Table H.6. Given our quantitatively small price effects, the

estimated in our data (see section 4.2), this approach does not necessarily increase power.

30

differences between these and the real estimates presented in Table 5 are mainly due to the

moderate degree of overall price inflation during the study period.

The expenditure- and income-based measures of GDP we generate are based on unusually

rich underlying data, but each has potential limitations. In particular, each may misattribute

transactions between agents located in the study area and counterparties located outside. In

the expenditure case, the main concern is that we do not directly observe net exports (NXt).

Imports show up as expenditure but are not local GDP, while exports do not show up in

expenditure but are part of local GDP. To the extent that cash transfers decrease (increase)

net exports from the study area, our expenditure multiplier would overstate (understate) the

multiplier. Intuitively, we might expect net exports to fall following a large external income

transfer: since many local firms are retail establishments, imports of intermediate goods

(including packaged consumer goods ready for sale) would likely increase. This suggests

that the expenditure-based approach might be upwardly biased.43 Note that transactions

between agents within our study area are correctly accounted for: for example, if study village

A imports goods from study village B then the value of these goods should be included in

local GDP as they are produced within our study area. Of course, increases in net imports

could in part reflect increases in economic activity outside of the study area due to the cash

transfers, which our concept of the local multiplier does not capture but which are a part of

the broader impact of the intervention.

As a robustness check to gauge the magnitude of the potential bias in the expenditure-

based measure due to imports of intermediate inputs, we first assign each component in

the non-durable and durable expenditure measures to enterprise types at which the good

is most likely to be purchased (using revenue shares of different enterprise types, where

appropriate). As noted in Section 4.2, this conservative methodology yields an upper bound

of 20% of local spending that may reflect expenditure on imported intermediate goods. If

imports scale linearly with expenditure, this suggests a transfer multiplier of at least 2.01

on local expenditure alone (see Appendix H).

In the income case, potential bias could arise if there are changes in net wage income

(NFIt) earned outside the study area, since this is not considered part of local GDP. This bias

seems unlikely to be quantitatively important in our setting: 86% of all non-farm employees

are family labor (and therefore presumably overwhelmingly local), and among individuals

employed for a wage, only 6% report an employment contact address outside the study area.

43. Note that direct imports by households themselves are unlikely to increase because on average only10% of households report ever shopping at a market outside our study area, and overall the impacts we seeon household spending and local enterprise revenue are fairly similar, suggesting that consumer spendingwas quite localized. Similarly, non-farm businesses report only 5% of customers coming from outside thestudy area, and that share does not change significantly in response to treatment.

31

To the extent some bias remains, we would expect it to be negative (towards zero), if net

labor income earned outside the study area decreases in response to higher local business

revenue, employment and wages. This suggests that the income-based approach may yield

a lower bound on the multiplier. Consistent with this bounding logic, the estimated income

multiplier is somewhat smaller in magnitude than the expenditure multiplier.

Next, we examine how alternative estimates of effects over the first three quarters affect

the overall multiplier estimate. A conservative approach excludes effects on GDP during

the first three quarters after transfers arrive, which may be statistically attractive in a

mean squared error sense since it yields more precise, if surely somewhat downward biased,

estimates. Under this assumption, the expenditure (income) multiplier estimate is 2.04

(1.45), which is smaller than the preferred estimates in Table 5, as expected, and estimates

attain greater statistical significance (see Appendix Table H.4). An arguably more realistic

method utilizes the household consumption data from Haushofer and Shapiro (2016) for the

first three quarters post-transfer, as we did in the construction of the MPC discussed above.

This yields a larger estimated expenditure multiplier of 3.09, with the increase due to a

greater contribution from recipients’ non-durable consumption (see Appendix Table H.4).

When this refinement is combined with our preferred assumptions on input shares, the

expenditure multiplier estimate is 2.48 (Appendix Table H.5). Though it relies on additional

assumptions, some readers may prefer this estimate since it addresses several limitations in

measurement of the main expenditure multiplier estimate.

6 Welfare implications

Transfer multiplier estimates have typically been used for positive economic analysis, to pre-

dict how fiscal policy will affect output. Yet since output is not social welfare, how fiscal

policy affects welfare is a distinct issue. Classic derivations of fiscal multipliers from account-

ing relationships such as the “Keynesian cross” could not deliver parallel statements about

welfare as they were not grounded in models of individual preferences. While recent papers

have focused primarily on estimation (Ramey 2019), a few have examined the relationship

between fiscal multipliers and welfare in the context of micro-founded models, emphasizing

that multipliers need not be sufficient statistics for welfare or (consequently) for optimal

policy (Sims and Wolff 2018). In fact, Mankiw and Weinzierl (2011) construct examples

in which the interventions with the largest multipliers have the least impact on social wel-

fare. The program evaluation literature on cash transfers, meanwhile, has largely focused on

estimating behavioral responses without exploring what these mean for welfare.

Here we examine the broad channels through which transfers could affect household

32

welfare, and how these relate to the transfer multiplier. Let indirect utility function vipTi, T q

define the utility achieved by household i when it receives a (possibly zero) transfer Ti

while other eligible households in the area receive transfers of T each. We are interested in

characterizing how T affects the quantity T ˚i defined by vipT˚i , 0q “ vipTi, T q, in other words,

the transfer that would make household i indifferent between receiving T ˚i on the one hand,

and experiencing the intervention we study on the other. Notice that if there were no general

equilibrium effects, in the sense that vi did not depend on T , then we would simply have

T ˚i “ Ti, i.e., the tautology that the value of receiving a dollar is a dollar.

We think of vi as the value of some generic underlying optimization problem

vipTi, T q “ maxxi

uipxi, x´ipT qq s.t. xi P XpTi, T q (9)

Here ui represents preferences over variables xi which the household chooses from a set X,

as well as variables x´i chosen by others. This formulation delineates two ways in which T

can affect the utility of household i. First, it may change market outcomes that determine

the choice set X – for example, prices or income from various sources. We therefore need

to interpret the impacts on output that generate the transfer multiplier through this lens.

Second, it may change behaviors x´ipT q that affect i’s well-being without appearing in the

transfer multiplier (e.g., through externalities).

6.1 Market outcomes

An increase in (real) output must reflect some combination of (i) an increase in the employ-

ment of factors of production and (ii) an increase in their aggregate productivity. While the

latter represents an unambiguous welfare gain, the former comes at an opportunity cost –

the value of foregone leisure, for example, in the case of labor inputs, or of foregone present

consumption in the case of capital inputs. Appendix J provides a formal illustration of the

mapping from household welfare to aggregate output, emphasizing this point. The discus-

sion also illustrates how household welfare differs from household expenditure, which is often

used in the program evaluation literature as a proxy for well-being. Specifically, expenditure

does not take into account the opportunity cost of supplying labor (or other inputs), and

over any finite time interval incorrectly interprets dis-saving as a welfare gain.

A key question is thus the extent to which the output response we observe can be ex-

plained by increases in the supply of scarce factors of production. In the data, we find fairly

limited evidence of increases in the employment of either land, labor, or capital. Land is

in relatively fixed supply; agricultural households do not report owning or renting more of

it (Table A.5) and we would not expect it to be a limiting factor in the sectors in which

33

the output expansion is concentrated (namely, retail and manufacturing). Total household

labor supply does not change significantly (Table 2), though we do see a net shift out of

self-employment and into wage employment (Table A.4, Panel A), with the latter increasing

by 1.8 hours per person per week on average across recipients and non-recipients. These

estimates are not statistically different from zero, however, and even under generous as-

sumptions can explain only around a 5% increase in real output, well below the observed

response.44

As for capital, the non-agricultural enterprises that increased their output did not increase

investment in fixed capital (Table 3, row 7) and, while increasing inventories somewhat, actu-

ally decreased them slightly in proportion to sales (Table 3, row 6). Moreover, if investment

were driving output increases then we would expect to see these increases concentrated in

enterprises owned by recipients, who gained access to a new source of capital, but if anything

we find the opposite (Table A.3). Overall, the limited factor supply response suggests that

the bulk of the output response we estimate must be attributable to productivity gains,

and should thus be valued at roughly $1 per $1 in welfare terms. (We discuss productivity

further in Section 7.)

The distribution of benefits also matters for welfare to the extent we value more highly

expansions in the budget sets of poorer households. While transfers were targeted to rela-

tively poor households, we have seen that large spillovers accrued to their somewhat richer

neighbors. Indeed, we find no significant reductions in village-level Gini coefficients for con-

sumption expenditure or wealth in treatment villages, and a small and marginally significant

(p ă 0.1) increase for wealth in control villages (Table A.7). We also reject in most cases

the null that observed effects on Gini coefficients are equal to the counterfactual changes

we might have expected had there been no spillovers. Overall, the patterns underscore the

large spillover gains for non-recipient households: wealthier non-recipients benefit along with

recipients, on some dimensions so much that inequality may slightly increase.

Distributional effects could also work through prices; while the overall price level changed

only slightly, changes in relative prices could transfer value between net buyers and net

sellers of goods and services. However, as for the overall index, effects are muted across

all individual goods prices that we measured, with nearly all changes within a -1% to +1%

range, indicating that any redistributive effects via price changes are likely to be very small

(Figure A.6).

44. Specifically, an increase of 1.8 hours per person is a 7.7% increase in wage labor hours. Assuming aCobb-Douglas production function with a labor share of 2{3, and no productive value of time given up fromself-employment, this implies a 5.2% increase in real output.

34

6.2 Non-market outcomes and externalities

We measured several outcomes that do not enter into our multiplier calculation but that ar-

guably influence well-being or proxy for it, and may thus capture externalities either between

or within households (x´ipT q in Equation 9). Specifically, we examine indices for psycholog-

ical well-being, health status, food security, education, female empowerment, and security

from crime. Each index is the inverse-covariance-weighted sum of component z-scores signed

so that positive values indicate better outcomes.45 The index for psychological well-being

can be interpreted as a measure of overall well-being. The next four indices arguably capture

intra-household externalities, while security from crime is an inter-household externality.

For recipient households, we find positive and significant reduced-form effects for four of

the six indices: psychological well-being, food security, education and security. Estimates

are close to zero and not significant for health and female empowerment.46 Total effects

including spillovers are similar for all but the security index. For non-recipient households,

on the other hand, we find no significant effects except for a 0.1 SD increase in the education

index (p ă 0.10). We do not find evidence of adverse spillover effects for non-recipient

households on any index, with point estimates positive for all but the security index, which

is indistinguishable from zero (-0.02 SD, SE 0.07). Village public good provision was also

unchanged (Walker 2018).

Overall, this pattern of findings suggests that the most important welfare effects were

market-mediated, though of course there may be other external effects we did not measure.

A possible exception is the impacts on inequality noted above: to the extent that households

care about comparisons with neighbors, these may constitute a form of “psychic externality.”

7 Discussion: utilization of productive capacity

The results raise the question of which features of the local economy enabled it to respond

elastically to a large aggregate demand shock. While fully addressing this is beyond the

scope of the present project, we outline what can be said given available data.

Any explanation of these patterns must apply to the retail and manufacturing sectors

specifically, as it is here rather than in agriculture or services that output gains are concen-

trated (Table A.2). Moreover, it cannot rely on an increase in the employment of factors

of production, since we find little evidence of this (Section 6.1). It must instead reflect an

45. The first five of these were pre-specified as primary outcomes; the components of the security indexwere pre-specified as part of a family of outcomes, though combining them into an index was not. Detailson index construction and results for components are in Appendix A, and PAP details in Appendix I.

46. The latter (non)-result contrasts with Haushofer and Shapiro (2016) who found increases in femaleempowerment and reductions in domestic violence among households receiving a similar transfer.

35

increase in the utilization of factors employed, as well as in the throughput of intermediate

goods. This notion is consistent with our observation (during fieldwork) of the retail and

manufacturing enterprises in the area, which typically involve some degree of “on-demand”

production. A retail establishment, for example, requires premises and an employee to “mind

the shop,” but once these are in place the volume of goods it sells depends largely on con-

sumer demand. Similarly, many small-scale manufacturing enterprises require equipment

and staff to be in place but then produce only when customers arrive. In fact, about 60% of

manufacturing revenue accrues to just two enterprise types, grain mills and welding shops,

both of which largely operate in this way.

These examples suggest retail and manufacturing sectors in which there are important

inputs whose costs are fixed over the relevant ranges – e.g., a building, milling machinery,

or hiring an employee – and whose utilization thus depends on demand. While we did

not measure capacity utilization directly, some indirect evidence suggests the existence of

meaningful slack. The average non-agricultural enterprise saw just 1.9 customers per hour,

in between which other inputs (i.e., employee time, fixed capital, inventories, etc.) may sit

idle. For labor inputs in particular, 72% of non-agricultural enterprises have just a single

employee, which suggests that (due to integer constraints) the labor input is essentially fixed

over the relevant range.47

Given this structure of production, we would expect the revenue from additional sales to

be paid out to the suppliers of intermediate goods, the suppliers of elastic factors of produc-

tion (whose marginal product increased as they became better utilized), and to enterprise

owners to the extent they can extract economic profits. We do not directly measure pur-

chases of intermediates, but upper bounds for the expenditure-weighted share of intermediate

inputs in total sales are sizeable, at 58% in the retail and 18% in the manufacturing sector

(see Appendix H). We also see an increase in wage bills, which accounts for 26% of increased

revenue (Table 3). Estimated effects on profits, meanwhile, are positive but modest and not

statistically significant (and may in any case be better interpreted as returns to the owners’

capital or labor which, as usual, are difficult to distinguish from true economic profits).

While suggestive, this interpretation of the supply side response to a demand shock is

consistent with other recent findings. In Uganda, Bassi et al. (2019) find that employees

in on-demand manufacturing (e.g., welding, furniture-making) spend about 25% of time

“waiting for customers” or “eating and resting.” More broadly, it relates to the old idea

in development economics that it might be possible to expand production without notable

47. Note that while we do not observe a large response in reported labor supply, we are not measuringutilization of labor capacity at the intensive margin; e.g., we do not distinguish between the time a shopkeeperwaits for customers or serves them.

36

price inflation due to the availability of slack capacity. Classic arguments focused on “surplus

labor” due to artificially high wages (Lewis 1954), while here both labor and capital appear

to have been underutilized due to limited flexibility to scale their employment to match

demand. Local mechanisms to address this through better coordination, such as periodic

markets, do so imperfectly, leaving some degree of residual excess capacity.48

A deeper question is whether specific market failures contribute to slack capacity in

steady-state in rural Kenya. Here we speculate about possibilities and directions worthy of

future investigation. The most immediate explanation revolves around the small scale of

local market activity; for instance, a single grain mill typically serves each village. While the

capacity provided by the standard grinding machine and the worker staffing it may generate

positive profit for the owner, this capacity may also exceed average local demand, implying

excess steady-state capacity which could be engaged following a demand shock. The small

scale of local markets is itself likely to reflect the poor road quality and high transport

costs that characterize rural Africa (Foster and Briceno-Garmendia 2010). The same logic

suggests that multipliers could be smaller in cities due to their greater population density and

better transportation infrastructure, not to mention the fact that rural economies are often

relatively closed, with large shares of consumption coming in the form of locally produced

food and other basic necessities.

Contracting frictions and institutions may also affect local market structure and capacity.

For instance, Bassi et al. (2019) document a pattern of small industrial clusters in neighboring

Uganda, in which a dozen small carpentry firms producing nearly identical products may

co-exist in the same area. Each of these separately owned firms has one or at most a few

employees, and they are characterized by the slack labor capacity noted above. Consolidation

into fewer, larger firms – each better utilizing workers’ time and any installed machinery, and

run by a more capable manager – could conceivably reduce slack and free up labor to shift

to alternate activities. Further research on the legal, financial and output market frictions

that prevent horizontal integration of this kind would be useful.49

8 Conclusion

A large-scale cash transfer program in rural Kenya led to sharp increases in the consumption

expenditures of recipient households, and extensive broader effects on the local economy,

including large revenue gains for local firms (that line up in magnitude with household con-

48. A growing literature also finds evidence of excess capacity in rich countries, especially in periods ofrecession (Murphy 2017; Michaillat and Saez 2015; Chodorow-Reich 2019).

49. Another fruitful direction for further investigation is whether cash transfers triggered a productivity-enhancing re-allocation of factors of production across sectors and firms (Hsieh and Klenow 2009).

37

sumption gains), as well as similar increases in consumption expenditures for non-recipient

and recipient households approximately a year and a half after the initial transfers. Firms

do not meaningfully increase investment, and there was minimal local price inflation, with

precisely estimated effects of less than 1% on average across a wide range of goods. Two

independent calculations of the local transfer multiplier using consumption data and income

data yield estimates of approximately 2.4, and reject the hypothesis that the multipliers are

less than or equal to 1 with 90% confidence. Several suggestive patterns are consistent with

the existence of “slack” on the production side in our context, which may partially account

for the large estimated multiplier.

Concerns that cash transfer programs like the one we study could have adverse conse-

quences for non-recipients were not borne out in our setting. Firm revenues and non-recipient

households’ consumption expenditures rise substantially in areas receiving large cash trans-

fers; there is little price inflation; overall economic inequality does not increase meaningfully

in treated areas; nor are there negative effects in terms of domestic violence, health, educa-

tion, psychological well-being, and local public goods. Instead, the positive spillovers we find

suggest that RCTs of cash transfer programs that simply compare outcomes in treatment

versus control villages may understate true overall impacts by ignoring the general equilib-

rium effects that we capture (along the lines that Miguel and Kremer (2004) argue in the

context of a health program).

This study is among the first to exploit randomized controlled trial methods to directly

estimate macroeconomic parameters and more broadly capture large-scale aggregate effects

of a development program. The multiplier effects that we focus on here have been the

subject of intense interest since at least the seminal work of Keynes (1936). Our approach

thus provides a novel counter-example to the well-known critique that RCT methods are

not well-suited to studying the “big” questions in development economics (Bardhan 2005;

Easterly 2006; Deaton 2010). We demonstrate that there need not always be a trade-off

between a study’s rigor and its relevance: economics research can increasingly achieve both

(Muralidharan and Niehaus 2017; Burke, Bergquist, and Miguel 2019).

The extent to which the multiplier results apply to other settings merits further discus-

sion. They are likely particularly relevant for rural areas of low and middle income economies

that share structural and institutional features with Kenya, including many other African

settings. One open question is the extent to which targeting of particular types of house-

holds, and the distribution of spending propensities across households, affect the multiplier:

for example, spillover effects might have been more muted if the program had also targeted

transfers to some better-off households with lower marginal propensities to spend on local

goods than the poor rural households we study. A second issue is how the multiplier may

38

vary over the business cycle. It is noteworthy that we estimate a large multiplier during a

period when the Kenyan economy was experiencing steady economic growth, rather than a

recession; this suggests that any under-utilization of supply side capacity is not simply tem-

porary or cyclical in rural Kenya, but may be more persistent.50 All that said, the results do

not necessarily imply that “helicopter drops” of money as part of a scaled-up national cash

transfer program would yield similar results, taking into account potential differences across

rural and urban locations. The source of funding would also matter: simply printing money,

for example, would likely have different inflationary consequences than financing via foreign

contributions, as we study here (and is common for many social protection schemes).

Looking ahead, a traditional perspective in the case of an open economy with complete

markets is that the economy should eventually revert to its previous steady-state after a

local aggregate demand shock like the one we study ends, with only transient effects on

consumption and prices (Farhi and Werning 2016). However, other theoretical perspec-

tives from international trade, economic geography, and development (e.g., Marshall 1890,

Rosenstein-Rodan 1943, Murphy, Shleifer, and Vishny 1989, Krugman 1991), as well as the

liquidity traps literature, suggest there could be persistent local effects of a temporary cash

infusion, due to agglomeration effects, increasing returns, changes in income inequality, mar-

ket structure and firm specialization, and even shifts in the social networks of traders and

suppliers. Temporary cash transfers and other forms of assistance have also been shown to

have effects on long-run human capital accumulation and earnings (Bouguen et al. 2019;

Baird et al. 2016). An evaluation of long-run patterns of economic activity, firm dynamics,

migration, and household living standards in the sample communities would provide a valu-

able experimental test of these theories.

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42

Figure 1: Transfer multiplier over time

Cum

mul

ativ

e m

ultip

lier

Panel A: Expenditure multiplier

−

−

95%

90%

p = 0.04

p = 0.14

2.53

0.0

0.5

1.0

1.5

2.0

2.5

3.0

Cum

mul

ativ

e m

ultip

lier

Panel B: Income multiplier

−

−

95%

90% p = 0.1

p = 0.23

2.28

0.0

0.5

1.0

1.5

2.0

2.5

3.0

Cum

mul

ativ

e m

ultip

lier

Panel C: Both multipliers

0.0

0.5

1.0

1.5

2.0

2.5

3.0

−

−

95%

90%

p = 0.04

p = 0.15

2.4

−

−

95%

90%

p = 0.02

p = 0.07

Average Jointtest

Months since first transfer

Qua

rter

ly m

ultip

lier

estim

ates

−

−

−

−

−

−

−

−

−

−

−

−

−

−

−

−

−

−

−

−

ComponentsHH Non−Durable ExpenditureHH Durable ExpenditureENT InvestmentENT Inventory

Totalcontribution:

1.170.810.480.07

2.53

0.0

0.5

1.0

0 3 6 9 12 15 18 21 24 27

Months since first transfer

Qua

rter

ly m

ultip

lier

estim

ates

−

−

−

−

−

−

−

−

−

−

−

−

−

−

−

−

−

−

−

−

ComponentsENT ProfitsHH Wage BillENT Capital IncomeENT Taxes Paid

Totalcontribution:

1.470.680.090.04

2.28

0.0

0.5

1.0

0 3 6 9 12 15 18 21 24 27

Notes: Panel A shows the cumulative expenditure multiplier over the first 29 months after start of the transfers in the top panel, and the corresponding quarterly impulse

response function (IRF) in the bottom panel. The integral under this IRF yields our overall point estimate of 2.53. Colored areas below the IRF represent the different

components of expenditure and the adjacent table indicates their total (over time) contribution. Darker shading indicates cases where a component turns negative in a given

quarter, leading some areas to overlap. Brackets around the quarterly IRF point estimates indicate ˘1SE confidence intervals obtained from 2000 wild bootstrap replications.

Whiskers below the overall point estimate indicate one-sided confidence intervals from the same bootstrap procedure, with p-values corresponding to tests of the one-sided

hypotheses H0 : M ă 0 and H0 : M ă 1 presented at the horizontal lines at 0 and 1 respectively. Panel B repeats the same exercise for the income multiplier. Panel C presents

results from aggregating the two estimators either by averaging them (left-hand side) or testing the joint null that both are less than the indicated critical values (right-hand

side). In each case whiskers indicate one-sided confidence intervals obtained via the bootstrap as above.

43

Table 1: Expenditures, Savings and Income

(1) (2) (3) (4)

Recipient Households Non-recipient Households

1pTreat villageq

Reduced form

Total Effect

IV

Total Effect

IVControl, low saturation

mean (SD)

Panel A: ExpenditureHousehold expenditure, annualized 292.98˚˚˚ 338.16˚˚˚ 333.73˚˚˚ 2,536.86

(60.09) (109.36) (123.24) (1,934.09)

Non-durable expenditure, annualized 186.96˚˚˚ 226.74˚˚ 316.62˚˚˚ 2,471.49(58.55) (99.62) (119.79) (1,877.82)

Food expenditure, annualized 71.61˚ 133.55˚˚ 132.84˚˚ 1,578.43(36.93) (63.98) (58.58) (1,072.31)

Temptation goods expenditure, annualized 6.51 5.88 −0.71 37.10(5.79) (8.82) (6.50) (123.59)

Durable expenditure, annualized 95.18˚˚˚ 109.07˚˚˚ 8.41 59.44(12.64) (20.23) (12.50) (230.90)

Panel B: AssetsAssets (non-land, non-house), net borrowing 178.09˚˚˚ 182.01˚˚˚ 132.63˚ 1,132.15

(24.61) (44.25) (78.32) (1,420.22)

Housing value 372.78˚˚˚ 480.68˚˚˚ 72.58 2,033.72(25.25) (38.88) (215.70) (5,030.37)

Land value 50.86 153.09 572.07 5,030.72(186.08) (262.48) (458.28) (6,607.61)

Panel C: Household balance sheetHousehold income, annualized 77.62˚ 134.02 229.46˚˚˚ 1,023.45

(43.66) (93.83) (88.59) (1,634.70)

Net value of household transfers received, annualized −1.68 −7.44 8.75 130.18(6.81) (13.06) (19.10) (263.75)

Tax paid, annualized 1.95 −0.09 1.66 16.93(1.28) (2.02) (2.02) (36.51)

Profits (ag & non-ag), annualized 24.70 33.73 44.08 485.20(23.18) (48.95) (45.35) (787.10)

Wage earnings, annualized 42.51 73.72 182.99˚˚˚ 495.37(32.24) (60.83) (65.44) (1,231.56)

Notes: Column 1 reports the coefficient on an indicator for treatment village from a regression using data from eligible households (as classified by the GE census team), andincludes an indicator for saturation status of the sublocation (Equation 1). Column 2 reports the total effect on treated households (eligible recipients) from the “optimal”IV spatial regression of each outcome on the amount transferred per capita to a household’s own village v (instrumented by village treatment status), and to villages otherthan v in each 2km radii band around the household (instrumented by the share of eligible households assigned to treatment in villages other than v inside the buffer), asin Equation 2. For this analysis, the sample is restricted to eligible households, including between 5,372 and 5,424 observations. Column 3 presents the average spillovereffect on eligible households in control villages as well as ineligible households (5,448 to 5,509 observations), coming from a stacked spatial regression of each outcome onthe amount transferred per capita GDP to each 2km radii band around each household (instrumented by the share of eligibles assigned to treatment in each buffer), asin Equation 3. The reported average effect comes from a population-share-weighted average effect experienced by those two groups, and is representative of the averageuntreated household. The number of radii bands included in Columns 2 and 3 is chosen, as pre-specified, by minimizing the BIC. Column 4 reports the weighted mean andstandard deviations of the outcome variables in low-saturation control villages (across eligible and ineligible households). Each regression is weighted by inverse samplingweights and contains baseline values of the outcome when available. Standard errors are clustered at the sublocation in Column 1, and calculated following Conley (2008)using a uniform kernel out to 10 km in Columns 2 and 3. * denotes significance at 10 pct., ** at 5 pct., and *** at 1 pct. level.

44

Table 2: Input Prices and Quantities

(1) (2) (3) (4)

Recipient Households Non-recipient Households

1pTreat villageq

Reduced form

Total Effect

IV

Total Effect

IVControl, low saturation

mean (SD)

Panel A: LaborHourly wage earned by employees 0.11˚˚˚ 0.04 0.19˚ 0.70

(0.03) (0.04) (0.10) (0.89)

Household total hours worked, last 7 days 2.44 1.41 −4.70 63.20(1.71) (3.69) (3.17) (54.14)

Panel B: LandLand price per acre 166.84 365.44 556.83 3,952.86

(201.20) (290.86) (412.34) (3,148.52)

Acres of land owned −0.19 −0.10 0.08 1.42(0.14) (0.09) (0.10) (2.37)

Panel C: CapitalLoan-weighted interest rate, monthly −0.01 0.01 −0.01 0.06

(0.01) (0.01) (0.01) (0.07)

Total loan amount 5.55 3.13 6.36 80.61(4.95) (8.34) (13.21) (204.36)

Notes: Column 1 reports the coefficient on an indicator for treatment village from a regression using data from eligible households (as classified by the GEcensus team), and includes an indicator for saturation status of the sublocation (Equation 1). Column 2 reports the total effect on treated households (eligiblerecipients) from the “optimal” IV spatial regression of each outcome on the amount transferred per capita to a household’s own village v (instrumented byvillage treatment status), and to villages other than v in each 2km radii band around the household (instrumented by the share of eligible households assignedto treatment in villages other than v inside the buffer), as in Equation 2. For this analysis, the sample is restricted to eligible households, including between2,828 and 5,423 observations for variables at the household level, and 2,832 observations at the individual level for wages. Column 3 presents the averagespillover effect on eligible households in control villages as well as ineligible households, coming from a stacked spatial regression of each outcome on the amounttransferred per capita GDP to each 2km radii band around each household (instrumented by the share of eligibles assigned to treatment in each buffer), as inEquation 3. We have between 2,781 to 5,509 observations at the household level and 2,391 wage observations at the individual level. The reported averageeffect comes from a population-share-weighted average effect experienced by those two groups, and is representative of the average untreated household. Thenumber of radii bands included in Columns 2 and 3 is chosen, as pre-specified, by minimizing the BIC. Column 4 reports the weighted mean and standarddeviations of the outcome variables in low-saturation control villages (across eligible and ineligible households). Each regression is weighted by inverse samplingweights and contains baseline values of the outcome when available. In addition, prices are quantity-weighted. That is, wages are weighted by the number ofhours worked, land prices by the number of acres purchased, and interest rates by size of each loan. Standard errors are clustered at the sublocation in Column1, and calculated following Conley (2008) using a uniform kernel out to 10 km in Columns 2 and 3. * denotes significance at 10 pct., ** at 5 pct., and *** at 1pct. level.

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Table 3: Enterprise Outcomes

(1) (2) (3) (4)

Treatment Villages Control Villages

1pTreat villageq

Reduced form

Total Effect

IV

Total Effect

IVControl, low saturation

weighted mean (SD)

Panel A: All enterprisesEnterprise profits, annualized 10.46 67.53 32.91 323.39

(24.35) (41.62) (37.27) (691.12)

Enterprise revenue, annualized −10.05 356.81˚˚ 244.27˚˚ 758.52(103.02) (144.21) (108.96) (2,493.40)

Enterprise costs, annualized −11.41 97.39˚˚ 79.48˚˚ 147.73(29.73) (38.27) (39.42) (550.11)

Enterprise wagebill, annualized −14.72 81.69˚˚ 70.49˚ 120.62(26.48) (33.76) (36.52) (492.11)

Enterprise profit margin 0.01 −0.06˚˚ −0.06˚˚˚ 0.44(0.02) (0.02) (0.02) (0.61)

Panel B: Non-agricultural enterprisesEnterprise inventory 11.01 34.68˚˚ 16.91 192.98

(9.14) (14.73) (10.80) (504.76)

Enterprise investment, annualized 4.00 13.58 6.82 178.25(7.05) (15.39) (8.65) (640.98)

Panel C: Village-levelNumber of enterprises 0.01 0.02 0.01 1.12

(0.01) (0.01) (0.01) (0.14)

Notes: Column 1 reports the coefficient on an indicator for treatment village, and includes an indicator for saturation status of the sublocation.Column 2 reports the total effect on enterprises in treatment villages (own-village effect plus across-village spillover) from the “optimal” IVspatial regression of each outcome on the amount transferred per capita to a enterprise’s own village v (instrumented by village treatmentstatus), and to villages other than v in each 2km radii band around the enterprise (instrumented by the share of eligible households assignedto treatment in villages other than v inside the buffer). Column 3 reports the total effect on enterprises in control villages (across-villagespillover only). For each Column, we stack 3 separate regressions for own-farm enterprises, non-agricultural enterprises operated within thehousehold, and non-agricultural enterprises operated outside the household, due to our independent sampling across these enterprise categories(Equations 10 and 11). We have between 9,997 and 10,254 observations for all enterprises, and 2,389 to 2,398 for variables we collect for non-agenterprises only, and 653 villages. The number of radii bands included in Columns 2 and 3 is chosen, as pre-specified, by minimizing the BIC.Column 4 reports the weighted mean and standard deviations of the outcome variables in low-saturation control villages (across all enterprisecategories). Each regression is weighted by inverse sampling weights and contains village-level baseline averages of the outcome variable byenterprise category when available. For monetary values, we convert effects to a per-household level by multiplying the average effect perenterprise in each enterprise category by the number of enterprises in that category, dividing by the number of households in our study area,and summing over all enterprise categories. For the number of enterprises, we run regressions at the village level, where the outcome is thenumber of enterprises per household in each category, we weight by the number of households in each village and sum up over all enterprisecategories. For the profit margin, we weight the effects across all enterprise categories by their share in the economy, and across each enterpriseby revenue, so that our estimate represents the effect on the revenue-weighted average enterprise in the economy. Standard errors are clusteredat the sublocation in Column 1, and calculated following Conley (2008) using a uniform kernel out to 10 km in Columns 2 and 3. * denotessignificance at 10 pct., ** at 5 pct., and *** at 1 pct. level.

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Table 4: Output Prices

(1) (2) (3) (4)

Overall Effects ATE by market access

ATEAverage maximum

effect (AME) below median above median

All goods 0.0010˚ 0.0042 0.0017˚ 0.0007(0.0006) (0.0031) (0.0009) (0.0007)

By tradability More tradable 0.0014 0.0062 0.0023 0.0021(0.0015) (0.0082) (0.0023) (0.0018)

Less tradable 0.0009 0.0034 0.0015 0.0001(0.0006) (0.0032) (0.0011) (0.0008)

By sector Food items 0.0009 0.0036 0.0016 0.0002(0.0006) (0.0033) (0.0012) (0.0008)

Non-durables 0.0014 0.0061 0.0026 0.0019(0.0017) (0.0089) (0.0026) (0.0019)

Durables 0.0019˚ 0.0070 −0.0009 0.0034˚˚

(0.0011) (0.0061) (0.0011) (0.0016)

Livestock −0.0008 −0.0027 −0.0008˚ −0.0017(0.0010) (0.0052) (0.0004) (0.0020)

Temptation goods −0.0011 −0.0112 −0.0008 −0.0003(0.0026) (0.0143) (0.0036) (0.0035)

Notes: Each row represents a regression of the logarithm of a price index on the “optimal” number of lags and distancebuffers of per capita Give Directly transfers in each buffer. Price indices are based on 311,138 non-missing price quotes for 70commodities and products. For each product, we take the logarithm of the median price quote in a market-month, and createour market price indices as an expenditure weighted average of these median price quotes across all goods in that market-month. Regressions include a panel of 1,734 market-by-month observations. The number of radii bands and lags is chosensequentially by minimizing the BIC, as pre-specified, for the overall price index, which selects a 4km radius; subcomponentsuse this value as well. Regressions include a full set of market and month fixed effects. Column 1 reports the implied ATE,calculated by evaluating the “optimal” regression specification at the average level of treatment intensity between September2014 and March 2017, the time during which transfers went out. Column 2 reports the average maximum effect, calculatedat the average across all markets of the month in which the largest per capita transfers went into a market’s neighborhood(up to the largest buffer selected by the algorithm). Columns 3 and 4 break down the ATE by market access, defined as

MAm “ř10r“0 r

´θNr, where θ “ 8 and Nr is the population in in the r ´ 2 to r km buffer around each market. Standarderrors (in parentheses) are as in and we allow for spatial correlation up to 10km and autocorrelation up to 12 months. *denotes significance at 10 pct., ** at 5 pct., and *** at 1 pct. level.

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Table 5: Transfer Multiplier Estimates

(1) (2) (3)M

EstimateH0: M ă 0

p-valueH0: M ă 1

p-value

Panel A: Expenditure multiplier 2.53 0.04˚˚ 0.14(1.42)

Household non-durable expenditure 1.17 0.19(1.32)

Household durable expenditure 0.81 0.00˚˚˚

(0.05)

Enterprise investment 0.48 0.13(0.42)

Enterprise inventory 0.07 0.02˚˚

(0.03)

Panel B: Income multiplier 2.28 0.10˚ 0.23(1.73)

Enterprise profits 1.47 0.13(1.28)

Household wage bill 0.68 0.27(1.15)

Enterprise capital income 0.09 0.31(0.17)

Enterprise taxes paid 0.04 0.08˚

(0.03)

Panel C: Expenditure and income multipliers

Average of both multipliers 2.40 0.04˚˚ 0.15(1.38)

Joint test of both multipliers 0.02˚˚ 0.07˚

Notes: Results are from the joint estimation of expenditure and income multipliers. Column 1 reportspoint estimates of both multipliers and their respective components. Each component is estimatedindividually and the multiplier is obtained by aggregating components as described in the main text.Effects of the cash infusion on flow variables (non-durable consumption, investment, wages, profits,capital income, and taxes) are obtained by dynamically estimating effect sizes over 29 months afterthe first transfer and computing the integral under this curve (Equation 7). Effects on remainingstock variables are the estimated the total endline treatment effects (Equations 2, 3 and 11). Transferamounts and outcome variables are deflated to January 2015 using the overall consumer price indexin the geographically closest market. Standard errors are computed from 2,000 replications of awild clustered bootstrap, which re-allocates within-sublocation Rademacher-perturbed residuals fromthe main population regressions to fitted outcome values to create perturbed samples. Columns 2and 3 conduct one-sided tests of each multiplier estimate M against 0 and 1 respectively, using thebootstrapped distributions of M. Panel C conducts two tests regarding both multipliers. The first rowcomputes the average of both estimates and conducts tests on this average using the same bootstrapprocedure. The last row reports p-values from joint tests of both multipliers against the same nulls.* denotes significance at 10 pct., ** at 5 pct., and *** at 1 pct. level.

48